Immersive Virtual Reality and Chronic Back Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Immersive Virtual Reality and Chronic Back Pain (NCT04307446), a randomized na study. The primary outcome is Pain Numerical Rating Scale.

2. Clinical Question

The clinical question is whether immediate changes in pain intensity differ after a 10-minute immersive virtual reality session compared with a 20-minute session among people with chronic back pain. The registry describes an exploratory feasibility study that also considered symptoms, affect, tolerance to cutaneous stimuli, and possible carryover after the experimental session. The posted primary outcome is change in pain intensity from before to immediately after the intervention.

This is a question about the observed immediate changes in this small feasibility study, not a definitive test of treatment effectiveness. Although the registry describes counterbalanced session order, the posted summary does not explain how the analysis handled within-person dependence, order, or possible carryover. Those details matter when interpreting a crossover comparison and are not reported in the registry record.

3. Trial Design

The registry records a completed, randomized crossover study sponsored by Tufts University. Its recorded start date is 2021-05-01, and its primary completion date is 2022-07-06. The registry lists enrollment as 23, while the brief summary describes a plan to recruit 20 adults. The reason for this difference is not reported in the registry record.

The brief summary describes multiday baseline assessments using ecological momentary assessment, followed by an experimental session containing two counterbalanced immersive virtual reality sessions: one lasting 10 minutes and one lasting 20 minutes. The registered sequences reflect both possible orders. Outcomes were described as measured immediately after each session, with symptom and affect monitoring by ecological momentary assessment for 72 hours after the experimental session to assess possible carryover. The description also mentions quantitative sensory testing for tolerance to cutaneous stimuli.

There is a difference in how the record characterizes the study: it labels allocation as randomized and the model as crossover, while the brief summary calls it a single-arm trial. The record does not explain this terminology. The posted outcome summaries present results under separate duration labels, but do not make clear whether all enrolled participants completed both sessions or whether every participant contributed to each reported outcome.

Masking is listed as none. The registry does not report details about allocation concealment, session washout, missing observations, the analysis population, or the statistical method used to account for the crossover structure. These are important design and analysis details, so they should not be inferred from the presence of randomized session order alone. Phase is listed as not applicable.

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 Pain Numerical Rating Scale, measured over Change in Pain Intensity from before to immediately after intervention.

The primary endpoint is the change in pain intensity from before to immediately after the intervention. Pain intensity was measured with a numerical rating scale running from 0 to 10; the registry describes a lower score as better. The posted results summarize this continuous outcome as a mean change with a standard deviation for each session duration.

Change scores are used to describe how a measure shifts between a baseline assessment and a later assessment. Comparing these changes can focus attention on the immediate response during each session rather than on pain levels at only one time point. In a crossover design, each participant may experience both conditions, which can make within-person comparison useful because a person can serve as their own reference. That advantage depends on an analysis that appropriately accounts for the repeated measurements and any order or carryover effects. The registry record does not report how those features were handled in the posted comparison.

The endpoint is appropriate for describing immediate subjective pain intensity, but it does not by itself capture longer-term symptoms, function, or sustained effects. The study description includes follow-up monitoring, yet the posted primary endpoint is specifically the change measured immediately after intervention. The record does not report a primary endpoint result for the longer monitoring period.

7. Results Posted in the Registry

• 20 Minutes: mean 1.10 versus 0.80 on control; difference 0.30 (95% CI -1.34 to 1.94), standardized effect d = 0.11; z-test p = 0.720.

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.

PROMIS Fatigue

• 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:
  • 20 Minutes: mean -0.50 versus 0.10 on control; difference -0.60 (95% CI -1.26 to 0.06), standardized effect d = -0.55; z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 20 Minutes and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies PANAS and PROMIS Fatigue as secondary outcomes. Quantitative summary results are posted for PROMIS Fatigue, while numerical PANAS results are not reported in the registry record. The broad pattern across the available secondary information therefore cannot be fully assessed across all listed outcomes.

The fatigue comparison has a different estimated direction from the primary pain comparison, and its confidence interval includes zero. This does not establish a reliable secondary effect or contradict the primary result. Different outcomes measure different aspects of experience, and estimates can vary in direction by chance, measurement variability, or other factors. The registry does not report enough about the analysis plan to establish which secondary outcomes were designated for formal hypothesis testing or how they relate hierarchically to the primary endpoint.

Secondary findings generally carry less weight than a prespecified primary result when there are multiple outcomes or comparisons. Testing many outcomes can increase the chance of obtaining a seemingly notable result by chance. Adjustments for multiplicity or a prespecified testing sequence can address that concern, but neither is reported in the registry record. The posted unadjusted results should therefore be viewed as exploratory rather than as independent confirmation.

The registry lists five outcome measures and two secondary outcomes, while reporting zero analyses. This combination leaves the full results and analysis context unclear. The results available for one secondary measure can be described, but they cannot establish a consistent pattern across all planned outcomes. Nor can the absence of posted numerical results for another outcome be interpreted as no change or no effect.

Overall, the available secondary information adds context about fatigue but does not strengthen a definitive conclusion about the primary pain comparison. The registry record does not report multiplicity handling, complete results for all listed secondary outcomes, or a prespecified analysis hierarchy. Those gaps are reasons to keep secondary interpretations cautious.

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

• PANAS
• PROMIS Fatigue

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical interpretation starts with identifying the outcome, the comparison, and the scale of the estimate. The primary outcome is a continuous change score for pain intensity. The posted comparison is the mean change after the 20-minute session relative to the mean change after the 10-minute session. A mean difference expresses how far apart the two reported group means are on the outcome scale. It is not a percentage change and does not describe how every participant responded.

What does a mean difference represent?

A mean is the arithmetic average of the recorded outcome values. For a change score, the average summarizes the observed shifts from before to immediately after intervention. The reported mean difference of 0.3 units is a comparison of those averages, not a count of people who improved or worsened. The standard deviations describe variation in individual changes around the means. They do not give the range of all observed values, and they should not be confused with a confidence interval for the mean difference.

General explanation: a mean difference is most useful when the outcome scale has a consistent interpretation across participants and conditions. Its clinical importance depends on context, including the scale and a meaningful-change threshold. A meaningful-change threshold is not reported in the registry record, so the estimate cannot be classified against such a benchmark from the posted information alone.

How should the confidence interval be understood?

A confidence interval gives a range of values that are reasonably compatible with the data and the method used to calculate it. The interval for the primary comparison includes zero and includes values on both sides of zero. Zero represents no average difference under the contrast as defined. Inclusion of zero means the data do not rule out no difference at the confidence level used for the interval; it does not show that the true difference is exactly zero.

General explanation: confidence intervals reflect sampling uncertainty under the assumptions of the calculation. They do not automatically incorporate uncertainty from measurement error, bias, missing data, or an incorrectly specified model. The registry record does not provide enough detail to evaluate all of those assumptions for the crossover analysis. The interval therefore helps describe statistical precision, but it cannot resolve design and analysis questions that are unreported.

What does the p-value add?

The posted unadjusted p-value is 0.72. A p-value measures how unusual data at least as incompatible with a 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 the probability that the result happened by chance. A large p-value does not demonstrate that the conditions are the same. It indicates that the reported data do not provide strong evidence against the null under the stated comparison and test.

The record labels this p-value unadjusted. No multiplicity adjustment is reported. The record also lists zero reported analyses, which leaves the analysis plan and any prespecified testing hierarchy unclear even though summary comparisons and an unadjusted p-value are posted. The statistical test used to produce the p-value is not reported in the registry record. The results should not be attributed to a particular test or model without that information.

Why does the crossover structure matter?

General explanation: crossover designs expose participants to more than one condition, so observations from the same participant are typically correlated. A paired analysis uses that within-person relationship; an unpaired analysis treats the condition groups as independent. The choice affects standard errors and confidence intervals. Session order and carryover can also affect comparisons if the response to an earlier condition persists into a later period.

The registry describes counterbalanced order, which means the two session sequences were represented in the design description. Counterbalancing alone does not establish that order effects or carryover were absent. The posted result does not state whether the calculation accounted for pairing, order, or period. Consequently, the posted summary can be described, but the analysis cannot be independently characterized as a particular crossover model based on the record.

The record gives outcome summaries for 21.0 participants in the 10-minute group and 20.0 in the 20-minute group for the primary measure. Those group figures should not be added to infer a number of distinct participants, particularly in a crossover study where participants may contribute to both conditions. The registry enrollment figure and outcome-specific group figures serve different descriptive purposes, and the record does not explain their relationship.

How should standard deviations be read?

General explanation: a standard deviation describes how dispersed observed values are around their mean. Larger dispersion generally makes an estimate less precise when the amount of information is otherwise similar. In a crossover comparison, the variability of within-person differences can be especially important; separate condition standard deviations do not reveal that paired variability. The registry posts a pooled standard deviation in the comparison details, but it does not describe how that quantity was used in the primary inferential analysis.

These methods concepts help distinguish the point estimate, its uncertainty, and the design assumptions behind the comparison. They do not fill in unreported analysis details. The most defensible reading is therefore descriptive: the posted estimate is small relative to its broad uncertainty, and the registry record does not document enough about the crossover analysis to make stronger claims.

11. Confidence Intervals and Precision

The primary comparison has a confidence interval from -1.339 to 1.939 units around a mean difference of 0.3 units. The interval covers zero and spans values in both directions. Thus, the point estimate alone gives an incomplete account: plausible values under the reported calculation include a lower mean change after the 20-minute session, no average difference, or a higher mean change. The data do not locate the difference precisely.

General explanation: a confidence interval is a measure of statistical precision, not a guarantee that the true effect lies within the interval. Its interpretation relies on the method and assumptions used to construct it. The record does not state the confidence level, the precise inferential method, or how the crossover pairing was incorporated. Those omissions limit a detailed audit of the interval.

The reported standard deviations also show variation in changes within each session-duration summary. Variation among individual responses can coexist with a modest difference between group means. In crossover data, however, separate standard deviations do not show the correlation between each participant's responses under the two durations. That within-person information can influence precision, and it is not reported in the registry record.

The interval should not be used as proof of equivalence. Equivalence requires a prespecified range of differences considered acceptably similar and a confidence interval assessed against that range. No such margin is reported. The primary result is best described as uncertain and not precise enough to establish a distinct difference or sameness between durations.

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, not the study's original design calculation. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is a stated fraction of the observed effect. The original trial's own sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were correct. The 90% power column uses a higher target chance of detecting it and therefore gives a larger planning figure. These are prospective planning quantities, not observed outcomes or guarantees.

The rows express planning for 100%, 75%, and 50% of the observed effect. Smaller effects are harder to distinguish from random variation and require more participants under the same assumptions. The figures therefore rise as the target effect becomes smaller. The estimates are particularly sensitive to the observed effect used as their starting point; an uncertain effect estimate can produce unstable planning requirements.

This is not observed power. Observed power is not a useful substitute for interpreting the estimate and confidence interval after a study is complete. The planning illustration should instead be read as a conditional scenario for future study planning, not as evidence that this completed feasibility study was designed or powered according to these figures.

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 = 0.300; pooled standard deviation σ = 2.699.
2. n = 2 × (1.96 + 0.842)² × 2.699² / 0.300² = 1,270.8, rounded up to 1,271 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 <- 0.3                      # observed difference in means
sigma <- 2.69928765531832                     # 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(4307446)
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 = 1,271 (80% power), 1,702 (90% power)
 75% of observed effect: n per arm = 2,260 (80% power), 3,025 (90% power)
 50% of observed effect: n per arm = 5,084 (80% power), 6,806 (90% power)
power.t.test: 1271.8 
Simulated power at n = 1,271 per arm: 0.797 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, or comparisons are examined. Even when each statistical test uses a conventional threshold, testing more hypotheses creates more opportunities for a result to appear noteworthy by chance. A prespecified primary endpoint and a clear testing hierarchy help readers distinguish confirmatory analyses from exploratory ones.

The registry identifies pain intensity as the primary outcome and lists PANAS and PROMIS Fatigue among secondary outcomes. It also records five outcome measures and zero reported analyses. Quantitative summary results are available for the primary endpoint and PROMIS Fatigue, but numerical PANAS results are not reported in the registry record. A complete list of analyses, prespecified hypotheses, and any multiplicity adjustment is not reported in the registry record. The primary comparison's p-value is explicitly unadjusted.

Missing-data handling is also not reported in the registry record. The outcome summaries include group-specific numbers, but the record does not explain why those numbers differ from the enrollment figure or whether participants had missing measurements, withdrew, or were excluded from a particular analysis. No analysis population, such as all randomized participants or participants completing both sessions, is specified. The counts therefore should not be taken as evidence of a particular missing-data strategy.

For a crossover study, the registry also does not report how incomplete pairs were handled, whether both session measurements were required, or how period and carryover effects entered the analysis. These details can affect both the estimate and its uncertainty. The study description mentions post-session monitoring for possible carryover, but a description of monitoring does not establish that the primary comparison adjusted for carryover or that any such effect was absent.

These omissions do not make the posted values unusable as descriptive results, but they limit their inferential interpretation. Readers cannot determine whether outcome selection, missing observations, or the analysis strategy affected the reported comparisons. The registry record does not report a statistical analysis plan sufficient to resolve these concerns.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports zero serious adverse events in the 10-minute group and zero in the 20-minute group. It also reports zero other adverse events and zero deaths for each duration group. The corresponding numbers listed as at risk are 21 for the 10-minute duration and 20 for the 20-minute duration.

These are event counts in the registry record, not proof that no adverse experiences occurred outside the categories or reporting process captured there. The record does not provide event descriptions, severity details for non-serious events, or information about how adverse events were collected. The brief study description focuses on feasibility and immediate responses, but does not provide a detailed safety-monitoring method.

Because the design is described as crossover, a participant may have experienced both durations. The duration-specific figures should not be added to estimate a number of distinct participants. The registry does not explain whether event monitoring was attributed to a particular session or whether events could be associated with both conditions. The reported zero counts are therefore best read narrowly as no events recorded in the listed categories for the respective duration groups.

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

The posted results describe average immediate changes in pain intensity and fatigue after two immersive virtual reality session durations. For the primary pain outcome, the estimated mean difference is small relative to the uncertainty represented by its confidence interval. The interval includes zero, and the unadjusted p-value does not provide evidence of a clear difference under the reported comparison. These findings do not establish that the durations are equivalent, nor do they show that either duration has no effect compared with no intervention.

The study did not include a no-intervention or usual-care comparator in the posted duration comparison. It therefore addresses the relative comparison between the 10-minute and 20-minute sessions, not whether either session changes symptoms compared with what would have happened otherwise. The registry describes a feasibility study intended to assess initial effects; its results should be understood in that exploratory context.

Immediate change in a self-reported pain scale is only one aspect of a broader experience. It does not by itself establish a lasting change, improvement in function, or an effect on long-term health. Although the study description mentions monitoring symptoms and affect after the experimental session, the registry record does not provide a posted primary result for that follow-up period.

The uncertainty also reflects gaps in the reported analysis. The record does not explain how the crossover structure, session order, or possible carryover was handled, and it does not report missing-data methods or a meaningful-change threshold. These limitations mean that neither a statistically non-significant result nor the point estimate should be turned into a categorical claim about clinical benefit or lack of benefit.

The results are most appropriately treated as preliminary, descriptive evidence about the immediate comparison of session durations in this study. They may inform questions for further research, but the registry record alone cannot support broader claims about treatment effectiveness or safety beyond the recorded outcome summaries.

17. Why This Trial Matters Statistically

This study raises a useful statistical question: how should an immediate outcome comparison be interpreted when a feasibility study uses a crossover design and reports summary results without a detailed analysis description? The distinction between design and analysis is important. Counterbalancing session order can help distribute order effects, but it does not itself show how the repeated observations were modeled or whether carryover was considered.

The example also illustrates why a point estimate should be read together with its confidence interval. The estimated primary difference may appear modest, but the interval is broad enough to include values in either direction. A single estimate without its uncertainty can invite a stronger conclusion than the data warrant. Conversely, a non-significant p-value is not proof of equivalence.

Another statistical lesson concerns feasibility studies and planning. Planning illustrations based on an observed effect can demonstrate how required sample sizes change when a target effect becomes smaller. They are conditional scenarios, not retrospective evidence about the original design or the chance that the completed study would detect a true effect. The registry record does not report the original sample-size rationale.

Finally, the incomplete reporting of secondary results, multiplicity handling, missing data, and crossover methods shows why transparent reporting matters. Those details help readers judge whether the estimate and its uncertainty match the design and the question. In their absence, careful description of what the posted numbers do and do not establish is more informative than a categorical conclusion.

18. Limitations

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

Several limitations are specific to the way this trial is described and reported. The registry calls the study randomized and crossover, while the brief summary describes it as single-arm. The record does not reconcile those descriptions. The sequence descriptions show that participants were assigned to different orders of session duration, but the posted result does not explain whether the inferential comparison accounted for the fact that the same participant may have experienced both conditions.

The registry enrollment figure is 23, whereas the study summary describes a plan to recruit 20 adults. Outcome summaries give different group-specific figures, and the record does not explain whether these differences reflect enrollment, completion, missing measurements, or another issue. It does not report the analysis population or the handling of incomplete crossover pairs.

The registry reports no masking. The outcome is self-reported pain intensity, so knowledge of session duration could be relevant to responses. This observation does not establish that reporting was biased, but the record does not describe procedures to address expectancy or other influences on subjective ratings.

The primary outcome is immediate change, limiting what it can say about persistence. The study description mentions later monitoring, but the corresponding primary follow-up results are not reported in the registry record. Session washout, order effects, and the analysis of carryover are also not reported.

Finally, complete numerical results for all listed secondary outcomes, multiplicity handling, a statistical analysis plan, and a clinically meaningful difference threshold are not reported in the registry record. Together, these gaps limit how confidently the posted estimates can be interpreted or generalized.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Immersive Virtual Reality and Chronic Back Pain — NCT04307446.
• Registry record last updated 2023-08-15; status last verified 2023-08.
• Results first posted 2023-08-15.
• 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

NCT04307446 is a completed randomized study of immersive virtual reality and chronic back pain, sponsored by Tufts University. The registry records a crossover model, no masking, enrollment of 23, and an intended assessment of feasibility and initial effects. The study description includes counterbalanced 10-minute and 20-minute sessions.

The primary outcome is immediate change in pain intensity on a 0-to-10 numerical rating scale. The posted mean difference comparing the 20-minute with the 10-minute session is 0.3 units, with a confidence interval from -1.339 to 1.939 and an unadjusted p-value of 0.72. The estimate is uncertain and does not establish either a difference or equivalence.

Quantitative secondary results are posted for PROMIS Fatigue; numerical PANAS results are not reported in the registry record. Serious adverse events, other adverse events, and deaths are recorded as zero in the listed duration groups. Details about crossover analysis, missing data, multiplicity, and the original sample-size rationale are not reported in the registry record.