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Chapter 8. Practice and a Pre-Registered Test

Note

The checklist and the protocol in this chapter are for research and for reading the literature; they are not medical advice. The checklist cannot tell anyone whether to take up a practice; it can only help put the questions clearly when reading a claim. The protocol is a draft design for reference by independent research institutions and must be reviewed by an ethics committee, registered on a clinical-trial registry, and run by a qualified team. Any symptom of the pelvic, urinary, digestive or reproductive systems, and any chest tightness, palpitation, dizziness or breathlessness, should be assessed by a doctor first.

Part one: a four-step checklist

The first seven chapters condense into a four-step checklist for reading any claim that an attention practice improves some physiological state.

  1. The chain. How many links does the claim have? Is each link evidence, a model, or an analogy? Does any link run in the opposite direction to the mathematics it appeals to (Chapters 1 and 2)? Has a “proof” inside a model been taken for an empirical conclusion (Chapter 6)?
  2. Anatomy. Does the pathway named as the cause anatomically reach the organ named as the effect? Is the measurement used from the same system as the conclusion claimed (Chapter 4)?
  3. Identifiability. Can the measurement used determine, in principle, the quantity claimed? Is there a different set of parameters that would give the same measurement while implying a different conclusion (Chapter 6)?
  4. The form of the evidence. Is it a case or a controlled trial? If a case, how was the time of entry into practice decided, and was the autocorrelation handled (Chapter 6)? If a trial, was the control arm matched for duration, posture, attention and contact — or was it a waiting list (Chapter 3 and part two below)?

Applied to the chain set out at the start of this book, the checklist gives the table below. This is not an overall verdict on practice; it states how far that chain’s support extends on these four dimensions.

Step The situation of that chain What it can support
The chain Six links; the first runs backwards (an alarmed prior raises the posterior), the third adds no information (d′d' independent of gain), and the cost of the second (falling entropy rate, longer first passage) is not mentioned Fails as a statement of mechanism; survives as a suggestion that this class of practice may be useful, but for different reasons than it gives
Anatomy The vagus does not innervate the pelvic organs; the pelvic outflow is sacral, and the “sacral parasympathetic” is itself disputed The fourth link is a factual error; a conclusion about the pelvis cannot be supported by heart-rate variability
Identifiability Four parameter sets reproduce the same cardiac trace, implying mean visceral conductances from 0.506 to 0.884 “HRV rose, hence visceral perfusion was restored” is an assumption, not an inference; the cardiac channel identifies only the timing of the response
Form of evidence Mainly cases With no effect at all, a naive test declares benefit in 28.5 % of cases; likelihood ratio about 2.2, weak evidence

Part two: a pre-registered two-arm randomised controlled trial

The question and the design choices

In adults with elevated body vigilance, does a six-week practice of “attending to the inside of the body without interpreting it”, compared with an external-attention control practice structurally matched for duration, posture, breathing guidance, instructor contact and length of written material, give a lower body-vigilance score at week 6, and by at least the smallest effect of interest?

Six design choices, each following from a result in an earlier chapter.

First, a single primary comparison: the practice against the structurally matched active control. Not against a waiting list. The reason is that Goyal and colleagues’ systematic review found small to moderate effects for mindfulness-type programmes relative to active controls and much larger ones relative to non-active controls (Goyal et al. 2014), and Van Dam and colleagues set out the field’s problem with overstatement (Van Dam et al. 2018). A comparison with a waiting list measures whether doing something beats doing nothing, which is not the question this book asks.

Second, a single primary outcome: the week-6 body-vigilance score, by analysis of covariance with the baseline score and site as covariates (Vickers and Altman 2001; Senn 2006). No autonomic index is a primary outcome, for two independent reasons: the structural non-identifiability of program p09 in Chapter 6, and the respiratory confound of program p05 in Chapter 4 together with the reliability ceiling of program p14 below. Heartbeat counting is used as no outcome at all, for the reasons in Chapter 1 (Zamariola et al. 2018).

Third, the outcome is measured in independent assessments on another day, taking the mean of two. The reason is program p11 in Chapter 3: what is measured at the end of a session is mainly a fast process gone by the next day, and the direction of the confound depends on the spacing; program p14 gives the reason for taking two.

Fourth, a pre-specified negative-control outcome: a quantity the framework predicts should not change (a single general life-satisfaction item unrelated to interoception, say, or performance on a cognitive task unrelated to the practice). It does not enter the power calculation; its role is to detect a generic expectancy effect, because if it moves by half the primary effect then “everything moved” is the simpler explanation.

Fifth, expectancy and credibility must be measured and matched: the credibility/expectancy questionnaire (Devilly and Borkovec 2000) is administered to both arms in week 1 and enters the decision rule as a qualifier. A structurally matched control is not the same as an expectancy-matched control, and that can only be measured, not assumed.

Sixth, run by an independent institution: the protocol, analysis code and decision rule are publicly registered before the first participant is enrolled, and the author takes no part in recruitment, intervention, assessment or analysis.

Protocol

Element Specification
Conduct and registration Run by a research team unconnected with the author; ethics committee approval; registration on a public clinical-trial registry; written and reported to SPIRIT/CONSORT (Chan et al. 2013; Schulz, Altman, and Moher 2010); no recruitment from the author’s community, students or customers
Participants Aged 25–60; body-vigilance screening score at or above a pre-set cut-off; able to complete a daily practice record independently; excluding current panic disorder, post-traumatic stress disorder, psychotic or dissociative symptoms, epilepsy, severe cardiovascular or respiratory disease, pregnancy, and anyone in interoception-focused psychotherapy; all screening and exclusion judged by site clinical staff. Anyone with a somatic symptom is referred for assessment and not enrolled
Stratification By site, baseline body vigilance (two strata) and imagery vividness (two strata); the reason for the imagery stratum is given in Chapter 3: instructions centred on imagery do not apply to people without spontaneous visual imagery (Zeman, Dewar, and Della Sala 2015)
Randomisation Central web-based randomisation, 1:1, variable and undisclosed block sizes; stratification factors adjusted for in the analysis
Intervention arm A once-daily interoceptive-attention practice of fixed duration, with instructions to attend to internal bodily sensations and spontaneously arising imagery without interpreting or naming them; the daily number of sessions and the interval between them are fixed and recorded (the reason is program p11 in Chapter 3: spacing is a parameter of the intervention)
Control arm A structurally matched external-attention practice: the same duration, the same posture, the same breathing guidance, the same number and length of instructor contacts, the same length of written material, with the content being attention to external sounds or visual objects. Matching of posture and muscle tone is required, for the mechanical alternative explanation in the last section of Chapter 5
Blinding Participants cannot be blinded to the content of their practice, but are blinded to the study hypothesis: neither arm’s materials state an expected direction. Outcome assessors and statisticians are blinded; credibility and expectancy are measured in week 1 (Devilly and Borkovec 2000)
Primary outcome The week-6 body-vigilance score (the mean of two independent assessments in weeks 6 and 7); analysis of covariance with baseline score and site as covariates; primary comparison intervention against control
Negative-control outcome One pre-specified quantity unrelated to interoception; its estimate and interval are reported and it does not enter the power calculation
Secondary outcomes The subscales of the Multidimensional Assessment of Interoceptive Awareness (Mehling et al. 2012); imagery-stream transition entropy at weeks 2 and 6 (Miller–Madow, per-person mean, fixed sampling interval; Chapter 3, program p13); task-switching cost (the hypothesis of Chapter 2); RMSSD and high-frequency power in a free-breathing window, reported alongside the respiration rate from the same window (Chapter 4); adverse events, especially symptom worsening and dissociative experiences. All descriptive or exploratory
Sensitivity analyses Per-protocol analysis; multiple imputation under missing-at-random with scenario analyses departing from it; a pre-specified test of baseline body vigilance as an effect modifier (testing the boundary condition of Chapter 6: whether the practice ceases to help when the standing alarmed prior is high)
Equivalence reading If the primary effect falls within ±SESOI, it is reported as “no difference worth acting on” within an equivalence-testing framework, not as “no effect” (Lakens, Scheel, and Isager 2018)

Smallest effect of interest and sample size

The smallest effect of interest is set at 0.35 SD. The reasoning: half a standard deviation is a frequently cited empirical threshold for the minimal important difference (Norman, Sloan, and Wyrwich 2003), and 0.35 lies below it, a conservative (harder to reach) choice; below that difference it is not worth changing practice for the daily time it costs. The baseline-outcome correlation is taken as 0.60 and the single-occasion reliability as 0.75. All are planning assumptions to be checked in a pilot.

Consider reliability first, since it determines the scale of the whole trial.

Calculation

# Chapter 8. Reliability sets a ceiling on any effect a trial can see. If the
# primary outcome has reliability rho_xx, an observed standardised effect is
# attenuated:
#   d_observed = d_true * sqrt(rho_xx)
# and the sample size needed goes up as 1 / rho_xx. For an outcome averaged
# over k occasions, the Spearman-Brown formula gives the reliability of the
# average, so the program answers a design question: is it cheaper to add
# participants or to add measurement occasions per participant? Exact
# formulas, no simulation.
import math
from statistics import NormalDist

Z = NormalDist().inv_cdf

def n_per_arm(d, rho_xx=1.0, power=0.90, alpha=0.05, rho_base=0.0):
    """ANCOVA with a baseline covariate correlated rho_base with the
    outcome."""

    d_obs = d * math.sqrt(rho_xx)
    za, zb = Z(1 - alpha / 2), Z(power)
    return 2 * (za + zb) ** 2 * (1 - rho_base ** 2) / d_obs ** 2 + za ** 2 / 4

def spearman_brown(rho1, k):
    return k * rho1 / (1 + (k - 1) * rho1)

if __name__ == "__main__":
    # smallest effect of interest, SD units
    D = 0.35
    print(
        "Smallest effect of interest: {:.2f} SD. ANCOVA, two-sided 0.05, 90 %"
        " power,".format(D)
    )
    print("baseline-outcome correlation 0.60.\n")
    print("   reliability   attenuated d   n per arm   n for two arms")
    for r in (1.00, 0.90, 0.80, 0.70, 0.60, 0.50):
        n = n_per_arm(D, rho_xx=r, rho_base=0.60)
        print("   {:11.2f} {:14.3f} {:11d} {:16d}"
              .format(r, D * math.sqrt(r), math.ceil(n), 2 * math.ceil(n)))

    print("\nHalving reliability from 0.90 to 0.50 nearly doubles the trial")
    print("({} -> {} per arm)."
          .format(math.ceil(n_per_arm(D, 0.90, rho_base=0.60)),
                  math.ceil(n_per_arm(D, 0.50, rho_base=0.60))))

    print(
        "\nAdd occasions or add people? Single-occasion reliability 0.60; the"
    )
    print("outcome is the mean of k occasions, each costing one visit.")
    print(
        "\n   k   reliability of the mean   n per arm   total visits per arm"
    )
    best = None
    for k in (1, 2, 3, 4, 6, 8, 12):
        r = spearman_brown(0.60, k)
        n = math.ceil(n_per_arm(D, rho_xx=r, rho_base=0.60))
        visits = n * k
        if best is None or visits < best[1]:
            best = (k, visits)
        print("   {:2d} {:24.3f} {:11d} {:22d}".format(k, r, n, visits))
    print(
        "\n   Total visits are minimised at k = {} ({} visits per arm): extra"
        .format(best[0], best[1])
    )
    print(
        "   occasions buy reliability along a flattening Spearman-Brown curve"
        " while"
    )
    print(
        "   costing visits linearly. But if the scarce resource is PEOPLE"
        " rather"
    )
    print(
        "   than visits - the usual case when recruitment is the bottleneck"
        " - the"
    )
    print(
        "   ranking reverses: k = 2 cuts the sample from {} to {} per arm"
        " for one".format(
            math.ceil(n_per_arm(D, spearman_brown(0.60, 1), rho_base=0.60)),
            math.ceil(n_per_arm(D, spearman_brown(0.60, 2), rho_base=0.60)),
        )
    )
    print(
        "   extra visit each. The Chapter 8 protocol takes two occasions for"
        " that"
    )
    print(
        "   reason, and states the assumption rather than leaving it"
        " implicit."
    )

    print(
        "\nThe same arithmetic bounds the autonomic secondary outcomes."
        " Programme"
    )
    print(
        "p05 showed that RMSSD moves with breathing pattern; if a measure's"
    )
    print(
        "session-to-session reliability is 0.4 in free breathing, then even a"
        " true"
    )
    print(
        "0.35 SD effect appears as {:.2f} SD and needs {} per arm - more"
        " than the".format(
            D * math.sqrt(0.4), math.ceil(n_per_arm(D, 0.40, rho_base=0.60))
        )
    )
    print(
        "primary outcome. That is a second reason, besides the"
        " identifiability"
    )
    print(
        "argument of p09, for not making an autonomic index the primary"
        " outcome."
    )

    print("\nWhat reliability is needed for a given trial size? Inverting:")
    print(
        "   n per arm available   minimum reliability for 90 % power at"
        " 0.35 SD"
    )
    for n in (60, 80, 100, 140, 200):
        za, zb = Z(0.975), Z(0.90)
        need = 2 * (za + zb) ** 2 * (1 - 0.60**2) / ((n - za**2 / 4) * D**2)
        print("   {:19d}   {:.3f}{}".format(n, need,
              "  (not attainable: exceeds 1)" if need > 1 else ""))
# Smallest effect of interest: 0.35 SD. ANCOVA, two-sided 0.05, 90 % power,
# baseline-outcome correlation 0.60.
#
#    reliability   attenuated d   n per arm   n for two arms
#           1.00          0.350         111              222
#           0.90          0.332         123              246
#           0.80          0.313         139              278
#           0.70          0.293         158              316
#           0.60          0.271         184              368
#           0.50          0.247         221              442
#
# Halving reliability from 0.90 to 0.50 nearly doubles the trial
# (123 -> 221 per arm).
#
# Add occasions or add people? Single-occasion reliability 0.60; the
# outcome is the mean of k occasions, each costing one visit.
#
#    k   reliability of the mean   n per arm   total visits per arm
#     1                    0.600         184                    184
#     2                    0.750         148                    296
#     3                    0.818         136                    408
#     4                    0.857         130                    520
#     6                    0.900         123                    738
#     8                    0.923         120                    960
#    12                    0.947         117                   1404
#
#    Total visits are minimised at k = 1 (184 visits per arm): extra
#    occasions buy reliability along a flattening Spearman-Brown curve while
#    costing visits linearly. But if the scarce resource is PEOPLE rather
#    than visits - the usual case when recruitment is the bottleneck - the
#    ranking reverses: k = 2 cuts the sample from 184 to 148 per arm for one
#    extra visit each. The Chapter 8 protocol takes two occasions for that
#    reason, and states the assumption rather than leaving it implicit.
#
# The same arithmetic bounds the autonomic secondary outcomes. Programme
# p05 showed that RMSSD moves with breathing pattern; if a measure's
# session-to-session reliability is 0.4 in free breathing, then even a true
# 0.35 SD effect appears as 0.22 SD and needs 276 per arm - more than the
# primary outcome. That is a second reason, besides the identifiability
# argument of p09, for not making an autonomic index the primary outcome.
#
# What reliability is needed for a given trial size? Inverting:
#    n per arm available   minimum reliability for 90 % power at 0.35 SD
#                     60   1.860  (not attainable: exceeds 1)
#                     80   1.389  (not attainable: exceeds 1)
#                    100   1.109  (not attainable: exceeds 1)
#                    140   0.790
#                    200   0.552

Reliability sets the ceiling directly, because the observed standardised effect is attenuated to dobs=dρxxd_{\text{obs}} = d\sqrt{\rho_{xx}}, the classical attenuation formula of test theory (Nunnally and Bernstein 1994): at a smallest effect of interest of 0.35 SD, a reliability of 1.00 needs 111 per arm and a reliability of 0.50 needs 221. On “more people or more occasions”, the answer depends on which resource is scarce: counted in total visits, k=1k = 1 is cheapest; counted in people, k=2k = 2 brings each arm from 184 down to 148 for one extra visit. This protocol takes two occasions and states the assumption. The last section gives a useful inverse calculation: with only 100 per arm the required reliability exceeds 1, that is, 90 % power is unattainable however good the measurement — trials of this kind should not be run at insufficient scale.

Calculation

# Chapter 8. Sample size for the pre-registered two-arm trial. Single primary
# comparison: non-judgmental interoceptive attention against a structurally
# matched external-focus control. Single primary outcome: body-vigilance score
# at week 6 by ANCOVA (baseline score, site). Planning assumptions: SESOI 0.35
# SD, baseline-outcome correlation 0.60, single-occasion reliability 0.75,
# outcome = mean of 2 occasions, two-sided 0.05, 90 % power. Normal theory
# first, then a simulation with an integer-scored scale, a floor, and the
# screening cut-off that selects participants into the trial.
import math
import random
from statistics import NormalDist

Z = NormalDist().inv_cdf
D, RHO_BASE, REL1, K_OCC = 0.35, 0.60, 0.75, 2
ITEMS, ITEM_MAX = 12, 6                  # 12 items scored 0-6: range 0-72
# screening cut-off for elevated vigilance
SCREEN_MIN = 28

def reliability(k):
    return k * REL1 / (1 + (k - 1) * REL1)

def n_formula(d=D, rho_xx=1.0, rho_base=RHO_BASE, power=0.90, alpha=0.05):
    d_obs = d * math.sqrt(rho_xx)
    za, zb = Z(1 - alpha / 2), Z(power)
    return 2 * (za + zb) ** 2 * (1 - rho_base ** 2) / d_obs ** 2 + za ** 2 / 4

def invert3(S):
    a, b, c = S[0]
    d, e, f = S[1]
    g, h, i = S[2]
    det = a * (e * i - f * h) - b * (d * i - f * g) + c * (d * h - e * g)
    return [
        [(e * i - f * h) / det, (c * h - b * i) / det, (b * f - c * e) / det],
        [(f * g - d * i) / det, (a * i - c * g) / det, (c * d - a * f) / det],
        [(d * h - e * g) / det, (b * g - a * h) / det, (a * e - b * d) / det],
    ]

# population before screening, scale points
TRUE_MEAN, TRUE_SD = 26.0, 9.0

def one_trial(rng, n, delta_sd):
    """delta_sd is the true effect in SD units, applied to the treated arm."""
    rows = []
    delta = delta_sd * TRUE_SD
    err_sd = TRUE_SD * math.sqrt(1 - RHO_BASE ** 2)
    meas_sd = TRUE_SD * math.sqrt((1 - REL1) / REL1 / K_OCC)
    for arm in (1, 0):
        got = 0
        while got < n:
            lat_b = rng.gauss(TRUE_MEAN, TRUE_SD)
            obs_b = lat_b + rng.gauss(0, meas_sd)
            b = min(ITEMS * ITEM_MAX, max(0, round(obs_b)))
            if b < SCREEN_MIN:
                continue                 # screened out, as in the real trial
            lat_y = (TRUE_MEAN + RHO_BASE * (lat_b - TRUE_MEAN)
                     - delta * arm + rng.gauss(0, err_sd))
            y = min(
                ITEMS * ITEM_MAX, max(0, round(lat_y + rng.gauss(0, meas_sd)))
            )
            rows.append((arm, b, y))
            got += 1
    n2 = len(rows)
    mb = math.fsum(r[1] for r in rows) / n2
    X = [(1.0, float(r[0]), r[1] - mb) for r in rows]
    Y = [float(r[2]) for r in rows]
    S = [
        [math.fsum(x[i] * x[j] for x in X) for j in range(3)]
        for i in range(3)
    ]
    v = [math.fsum(x[i] * y for x, y in zip(X, Y)) for i in range(3)]
    inv = invert3(S)
    beta = [math.fsum(inv[i][j] * v[j] for j in range(3)) for i in range(3)]
    res = [
        y - math.fsum(bb * xx for bb, xx in zip(beta, x))
        for x, y in zip(X, Y)
    ]
    s2 = math.fsum(r * r for r in res) / (n2 - 3)
    df = n2 - 3
    z = Z(0.975)
    # Cornish-Fisher t quantile
    tcrit = z + (z ** 3 + z) / (4 * df)
    # sign: lower score is better
    t = -beta[1] / math.sqrt(s2 * inv[1][1])
    at_floor = sum(1 for r in rows if r[0] == 1 and r[2] == 0) / n
    return t > tcrit, at_floor

if __name__ == "__main__":
    rel = reliability(K_OCC)
    print(
        "outcome = mean of {} occasions; single-occasion reliability {:.2f}"
        " -> {:.3f}".format(K_OCC, REL1, rel)
    )
    n0 = n_formula(rho_xx=rel)
    print("normal theory: n = {:.3f} -> {} per arm (attenuated d = {:.3f})"
          .format(n0, math.ceil(n0), D * math.sqrt(rel)))

    rng = random.Random(2026)
    chosen = None
    print("\nsimulation with integer scores, a floor at 0 and the screening")
    print("cut-off at {}:".format(SCREEN_MIN))
    for n in (math.ceil(n0), 150, 165, 180):
        res = [one_trial(rng, n, D) for _ in range(1500)]
        pw = sum(r[0] for r in res) / len(res)
        se = math.sqrt(pw * (1 - pw) / len(res))
        fl = math.fsum(r[1] for r in res) / len(res)
        print(
            "   n = {:3d}/arm: power {:.3f} (s.e. {:.3f}); treated arm at"
            " floor {:.1%}".format(n, pw, se, fl)
        )
        if chosen is None and pw - 2 * se >= 0.90:
            chosen = n
    if chosen is None:
        chosen = 180
    t1 = sum(one_trial(rng, chosen, 0.0)[0] for _ in range(1500)) / 1500
    print("   smallest n with power - 2 s.e. >= 0.90: {}".format(chosen))
    print(
        "   error rate there with no effect: {:.3f} against a nominal 0.025,"
        " since".format(t1)
    )
    print(
        "   the simulated rejection counts only the favourable direction"
        " against a"
    )
    print(
        "   two-sided critical value; the reported trial test is two-sided at"
        " 0.05."
    )

    plan = math.ceil(chosen / 0.85)
    print(
        "\nplanned: {} analysable per arm; 15 % loss -> {} randomised"
        "\nper arm, {} in all".format(chosen, plan, 2 * plan)
    )

    print(
        "\nsensitivity, analysable per arm (normal theory, reliability"
        " {:.2f}):".format(rel)
    )
    print("   SESOI \\ rho_base      0.4     0.6     0.8")
    for d in (0.25, 0.35, 0.50):
        print("   {:4.2f} SD          ".format(d) + "".join(
            "{:8d}".format(math.ceil(n_formula(d=d, rho_xx=rel, rho_base=r)))
            for r in (0.4, 0.6, 0.8)))

    print(
        "\nThe trial is powered for the PRIMARY comparison only. The"
        " pre-specified"
    )
    print(
        "negative-control outcome (a measure the framework predicts"
        " should NOT"
    )
    print(
        "change) is reported with its interval and is not powered; its role"
        " is to"
    )
    print(
        "show whether a generic expectancy effect moved everything, and a"
        " change"
    )
    print(
        "there of similar size to the primary effect voids the primary claim."
    )
# outcome = mean of 2 occasions; single-occasion reliability 0.75 -> 0.857
# normal theory: n = 129.051 -> 130 per arm (attenuated d = 0.324)
#
# simulation with integer scores, a floor at 0 and the screening
# cut-off at 28:
#    n = 130/arm: power 0.847 (s.e. 0.009); treated arm at floor 0.1%
#    n = 150/arm: power 0.893 (s.e. 0.008); treated arm at floor 0.1%
#    n = 165/arm: power 0.915 (s.e. 0.007); treated arm at floor 0.1%
#    n = 180/arm: power 0.946 (s.e. 0.006); treated arm at floor 0.1%
#    smallest n with power - 2 s.e. >= 0.90: 165
#    error rate there with no effect: 0.021 against a nominal 0.025, since
#    the simulated rejection counts only the favourable direction against a
#    two-sided critical value; the reported trial test is two-sided at 0.05.
#
# planned: 165 analysable per arm; 15 % loss -> 195 randomised
# per arm, 390 in all
#
# sensitivity, analysable per arm (normal theory, reliability 0.86):
#    SESOI \ rho_base      0.4     0.6     0.8
#    0.25 SD               331     253     143
#    0.35 SD               170     130      74
#    0.50 SD                84      64      37
#
# The trial is powered for the PRIMARY comparison only. The pre-specified
# negative-control outcome (a measure the framework predicts should NOT
# change) is reported with its interval and is not powered; its role is to
# show whether a generic expectancy effect moved everything, and a change
# there of similar size to the primary effect voids the primary claim.

Normal theory gives 129.051 per arm, rounded to 130. The simulation then adds integer scoring, a floor at 0 and the screening cut-off: power is 0.847 at 130 per arm, 0.893 at 150, 0.915 at 165 and 0.946 at 180. By the rule “power minus two standard errors not below 0.90”, the plan takes 165 analysable per arm. Allowing 15 % loss to follow-up and non-assessability, 195 are randomised per arm, 390 in all. The sensitivity table shows that a smallest effect of interest of 0.25 SD would need 253 per arm, and that if the baseline-outcome correlation were only 0.40 a 0.35 SD effect would need 170.

Following the result in Volume 33, Chapter 6, “90 % power” means that when the true effect is exactly 0.35 SD, the probability of reaching a conclusion of the form “the practice is better” (a confidence interval excluding zero) is about 90 %; in that same situation the strongest conclusion, “better by at least 0.35 SD”, has only about a 2.5 % chance of appearing.

Decision rule

Calculation

# Chapter 8. Decision rule, fixed before unblinding. Primary comparison:
# non-judgmental interoceptive attention versus the structurally matched
# external-focus control. D = adjusted difference in the week-6 body-vigilance
# score (ANCOVA: baseline, site), expressed in SD units, with its 95 %
# confidence interval. NEGATIVE D favours the practice (a lower score is
# better). SESOI 0.35 SD. Gates, checked before anything else: more than 20 %
# of randomised participants without a primary outcome; allocation revealed to
# outcome assessors before database lock. Pre-specified qualifiers: the
# credibility/expectancy check (if the two arms differ by more than 1 point on
# a 9-point credibility scale, expectancy is not matched) and the
# NEGATIVE-CONTROL outcome (if it moved by at least half the primary effect, a
# generic expectancy effect is the simpler explanation). An adverse-event
# excess in either arm is reported first, whatever the efficacy result.
SESOI = 0.35

def verdict(d, lo, hi, missing=0.08, cred_gap=0.3, neg_ctrl=0.05,
            revealed=False, ae_excess=False):
    pre = "ADVERSE-EVENT SIGNAL REPORTED FIRST;\n" if ae_excess else ""
    for bad, why in (
        (
            missing > 0.20,
            "{:.0%} without primary outcome (limit 20 %)".format(missing),
        ),
        (revealed, "allocation revealed to assessors before lock"),
    ):
        if bad:
            return "{}D = {:+.2f}: NOT INTERPRETABLE - {}".format(pre, d, why)
    if hi <= -SESOI:
        v = "benefit of at least the SESOI"
    elif hi < 0:
        v = "benefit, but not shown to reach the SESOI"
    elif lo > 0:
        v = "the control arm did better"
    elif lo >= -SESOI and hi <= SESOI:
        v = "no difference worth acting on"
    else:
        v = "unclear: the interval is too wide to decide"
    notes = []
    if cred_gap > 1.0:
        notes.append(
            "credibility differed by {:.1f} points: expectancy is not"
            "\n      matched, so part of D may be expectancy".format(cred_gap)
        )
    # the negative control only qualifies a claimed benefit; with no benefit
    # to explain away there is nothing for it to undercut
    if hi < 0 and abs(d) > 1e-9 and abs(neg_ctrl) >= 0.5 * abs(d):
        notes.append(
            "negative control moved {:+.2f} SD, at least half of D:"
            "\n      a generic expectancy effect is the simpler explanation"
            .format(neg_ctrl)
        )
    out = "{}D = {:+.2f} ({:+.2f} to {:+.2f}): {}".format(pre, d, lo, hi, v)
    for n in notes:
        out += "\n    qualifier: " + n
    return out

CASES = [
    # clear benefit past SESOI
    (-0.52, -0.80, -0.38),
    # benefit, below SESOI
    (-0.22, -0.41, -0.03),
    # nothing worth acting on
    (-0.05, -0.24, 0.14),
    # control did better
    (0.30, 0.09, 0.51),
    (-0.20, -0.70, 0.30),                                    # too wide
    # expectancy not matched
    (-0.48, -0.74, -0.22, 0.08, 2.4),
    # negative control moved
    (-0.44, -0.70, -0.18, 0.08, 0.3, -0.26),
    # too much missing data
    (-0.50, -0.78, -0.22, 0.27),
    # adverse-event signal
    (-0.10, -0.29, 0.09, 0.08, 0.3, 0.02, False, True),
]

if __name__ == "__main__":
    for c in CASES:
        print(verdict(*c))
    print(
        "\nSecondary outcomes (the autonomic indices, the imagery-stream"
        " entropy of"
    )
    print(
        "p13, the questionnaire subscales) are reported with intervals and"
        " never"
    )
    print(
        "change the verdict. Per programme p09, no autonomic index is read as"
    )
    print(
        "evidence about visceral perfusion; per p05, every autonomic index is"
    )
    print(
        "reported alongside the respiration rate recorded in the same window."
    )
    print(
        "\nThe example numbers above are invented, to show what each branch"
        " prints."
    )
# D = -0.52 (-0.80 to -0.38): benefit of at least the SESOI
# D = -0.22 (-0.41 to -0.03): benefit, but not shown to reach the SESOI
# D = -0.05 (-0.24 to +0.14): no difference worth acting on
# D = +0.30 (+0.09 to +0.51): the control arm did better
# D = -0.20 (-0.70 to +0.30): unclear: the interval is too wide to decide
# D = -0.48 (-0.74 to -0.22): benefit, but not shown to reach the SESOI
#     qualifier: credibility differed by 2.4 points: expectancy is not
#       matched, so part of D may be expectancy
# D = -0.44 (-0.70 to -0.18): benefit, but not shown to reach the SESOI
#     qualifier: negative control moved -0.26 SD, at least half of D:
#       a generic expectancy effect is the simpler explanation
# D = -0.50: NOT INTERPRETABLE - 27% without primary outcome (limit 20 %)
# ADVERSE-EVENT SIGNAL REPORTED FIRST;
# D = -0.10 (-0.29 to +0.09): no difference worth acting on
#
# Secondary outcomes (the autonomic indices, the imagery-stream entropy of
# p13, the questionnaire subscales) are reported with intervals and never
# change the verdict. Per programme p09, no autonomic index is read as
# evidence about visceral perfusion; per p05, every autonomic index is
# reported alongside the respiration rate recorded in the same window.
#
# The example numbers above are invented, to show what each branch prints.

If any gate fails — more than 20 % of randomised participants without a primary outcome, or allocation revealed to assessors before database lock — the report reads “not interpretable” whatever the primary outcome. If serious adverse events are more frequent in either arm, the safety signal is reported first. Only when the upper bound of the confidence interval is at or below −0.35-0.35 SD does the report read “benefit of at least the smallest effect of interest”; when the upper bound is below 0 but above −0.35-0.35, “benefit, but not shown to reach the SESOI”; when the lower bound is above 0, “the control arm did better”; when the interval lies within ±0.35, “no difference worth acting on”; otherwise “unclear”. Two qualifiers: a credibility difference of more than 1 point means expectancy was not matched; and a negative-control change of at least half the primary effect means a generic expectancy effect is the simpler explanation.

What this trial cannot show

First, it tests one set of instructions, one duration and one six-week schedule, and does not generalise to other practices. Second, it does not test at all the physiological chain of Chapters 4, 5 and 6: it measures no visceral or pelvic blood flow and therefore can neither support nor refute any claim about visceral restoration. Testing that part would require a direct measurement of the visceral bed taken simultaneously with cardiac observation (Chapter 6), and this protocol contains no such measurement. Third, participants cannot be blinded to the content of their practice, so the contribution of expectancy can only be partly identified, through the negative control and the credibility measure, and not excluded. Fourth, the conclusions do not extend to people with somatic disease, panic disorder or post-traumatic stress disorder, who are excluded. Fifth, a six-week outcome does not answer the question of long-term effect. Sixth, if the result is “no difference worth acting on”, that is the trial’s conclusion, and secondary outcomes, subgroups or autonomic indices cannot be substituted for it.

Ethics and conflict of interest

Directing attention into the body makes symptoms worse for some people (Paulus and Stein 2010; Khalsa et al. 2018), so adverse-event collection must be active and must specifically include symptom worsening, panic attacks and dissociative experiences; an independent data and safety monitoring committee is appointed; participants may withdraw at any time; anyone developing a somatic symptom during the trial is referred for clinical assessment and withdrawn from the intervention. Whatever the result, the protocol, statistical analysis plan, analysis code and summary results will be published, with de-identified individual data available under a data-sharing statement; the author takes no part in recruitment, intervention, assessment or analysis.

Disclosure

The author uses the works of 5D Library, including this book, as the methodological basis of his community courses, the 5D Ascension Cards (Dimensional Shift Card Decks) and the Yafu AI knowledge base, and therefore has a commercial interest in the subject of this book. The author also teaches breathing, listening and attention practices in those community courses, and this book is about the mechanisms and the testing of exactly that class of practice, so the interest is direct. The book promotes no course, card deck or service and gives no practice prescription, duration or course length; the Chapter 8 trial is designed to be run and analysed by researchers independent of the author’s business and does not recruit from the author’s community, students or customers; all the code and the study protocol are published openly for anyone to check. The author provides no medical services and sells no device, supplement or test.

Summary

The four-step checklist reads claims that an attention practice improves a physiological state along four dimensions: the chain, the anatomy, identifiability and the form of the evidence. Applied to the chain set out at the start of this book, it shows that the first link runs backwards, the third adds no information, the fourth is a factual error, and the key parameter cannot be identified from the measurement used, while the case evidence carries a likelihood ratio of about 2.2. The pre-registered two-arm trial makes the practice against a structurally matched active control its single primary comparison and the week-6 body-vigilance score by analysis of covariance its single primary outcome, with a smallest effect of interest of 0.35 SD, 165 analysable and 195 randomised per arm, 390 in all; the outcome is measured in two independent assessments on another day, a negative-control outcome and a credibility/expectancy measure are pre-specified, and the decision rule is written as code. Autonomic indices and imagery-stream entropy are secondary outcomes only and are reported with the qualifications of the earlier chapters. The trial does not test the visceral blood-flow segment of the chain, and the book says so.

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Fan, Y. (2026). Interoceptive Decoupling, Salience-Network Switching and Autonomic Visceral Restoration: From Precision-Weighting in the Default Mode Network and the Redistribution of Vagal Tone to the Neurophenomenology of a Non-Judgmental Imagery Stream, with a Textual Examination of neiguan in the Huangdi Neijing [内感受解离、突显网络切换与内脏自主神经修复] (Version 1.0.0). 5D Library. https://doi.org/10.5281/zenodo.24020418 · Licensed under Creative Commons Attribution-NonCommercial-NoDerivatives 4.0 International (CC BY-NC-ND 4.0).