Where 0.31 comes from

A measure of consciousness has a problem that most medical tests do not. To check a blood test for diabetes, you compare it with a gold standard, such as a glucose tolerance test. For consciousness the only gold standard is the person’s own report, and the patients who most need the test are the ones who cannot give one. Any cutoff has to be set in people who can report and then carried over to people who cannot.

That is what Silvia Casarotto and colleagues did in a 2016 study in the Annals of Neurology. They first built a benchmark population of 150 subjects, healthy controls and communicative brain-injured patients, in various states of conscious wakefulness, disconnected consciousness and unconsciousness. They then applied the cutoff learned in that group to 81 patients who could not communicate, 38 in a minimally conscious state and 43 in a vegetative state.

Three kinds of report

The benchmark sorted every recording by what the subject could say about it. Some subjects gave an immediate report, because they were awake and talking: healthy people, and patients with strokes, the locked-in syndrome, or recent emergence from the minimally conscious state. Others gave a delayed report: they were unresponsive at the time, in REM sleep or under ketamine, and on waking they described experiences. A third group gave no report on waking from deep sleep or from anaesthesia with midazolam, xenon or propofol.

The study counted the first two groups as conscious and the third as unconscious. That choice is the foundation of everything that follows, and Part seven returns to its weak points. For now the important feature is that two kinds of conscious recording, REM dreaming and ketamine, come from people who were as unresponsive as any patient. Their bodies did nothing, and they still counted as conscious because of what they said later.

The numbers in the table

For each subject the team stimulated up to four sites, two over the frontal lobes and two over the parietal lobes, and took the highest PCI value across sites, called PCI_max. According to the full text, the reasoning was that a single island of complex cortex should count, and a parallel is drawn with using a patient’s best behavioural score. The table of PCI_max values in the paper shows a clean split.

In the unconscious conditions, PCI_max ranged from 0.15 to 0.31 in deep sleep, 0.23 to 0.31 under midazolam, 0.11 to 0.31 under xenon and 0.23 to 0.31 under propofol. In the conscious conditions, it ranged from 0.36 to 0.56 in REM sleep, 0.36 to 0.52 under ketamine and 0.39 to 0.70 in wakefulness. The brain-injured patients who could talk ranged from 0.34 at the lowest, in cortical stroke, to 0.61 at the highest.

The analysis that turns those ranges into a cutoff is called receiver operating characteristic analysis. It tries every possible threshold and records how many conscious recordings fall above it and how many unconscious ones fall below. In this benchmark the analysis found an empirical cutoff of 0.31, which in the authors’ words “discriminated between the unconscious and the conscious conditions with 100% sensitivity and 100% specificity”. Every unconscious maximum sat at or below 0.31, and every conscious maximum sat above it.

A minimal worked case

It helps to see the compression step on something small enough to do by hand. Take a toy brain with three sources and eight moments after the pulse, and read the table column by column: the three sources at moment one, then at moment two, and so on. Lempel–Ziv parsing moves along the string and starts a new phrase each time it meets a pattern it has not seen before. The fewer the phrases, the more compressible and predictable the pattern.

The authors’ own caution

The 2016 paper is unusually direct about the status of its cutoff. Its discussion says the cutoff “should not be interpreted as an absolute boundary between consciousness and unconsciousness, but rather should be used as an operational threshold” for conditions with no reliable behavioural reference. It also states that “the absolute PCI values necessarily depend on the specific data acquisition/analysis protocol”, naming the sampling rate, the type of source modelling and the statistics.

That sentence answers half of the question in this paper’s title. The value 0.31 is not special in itself. Another laboratory with a different pipeline would draw its line somewhere else, and what should carry across laboratories is the gap, if the gap is real. The other half of the question is why there is a gap at all, across such different states, and that is about physiology rather than statistics.

For Dr Menon, Part two sets a practical condition. If the research group’s pipeline matches the one validated in Milan, she can read their number against 0.31. If it does not, she should ask what their own benchmark looked like. Either way, she should ask how many sites they stimulated, because a single low value from one site is not the same result as a low maximum from four.

A toy cortex with a knock button

Parts three and four made two claims that are easy to state and hard to check in words. The first is that bistability, by itself, is enough to collapse the echo. The second is that a single number can hide what it depends on: the protocol, the number of trials and the place you knock. I built a small simulation to see whether both claims survive contact with an explicit model. It is a deliberately simplified toy, and nothing in it is a brain.

What the model contains

The model has 60 nodes arranged in six modules of ten, and each node passes a smoothed activity rate to others through random weights. Weights inside a module are strong, while long-range links between modules are sparse. The whole network is scaled so that it sits just below the edge of runaway activity, as cortex is thought to in waking, and every node receives a little random noise at each step.

A pulse to one module stands in for TMS, and three knobs set each condition. Gain scales every connection, and long-range strength removes a share of the links between modules, as a white-matter injury would. The third knob is adaptation: when a node is strongly driven it triggers an OFF-period, a slow silence in its output that also shows as a large deflection on the simulated electrode. That is the toy’s simplified version of the bistability Pigorini and colleagues recorded in human cortex.

The analysis follows the published outline of Casali and colleagues as closely as a toy allows. The response is averaged over 200 trials, and only deflections larger than anything seen in the pre-pulse baseline are kept. The resulting yes-or-no matrix, channels by time, is compressed with the Lempel-Ziv method and divided by the value expected for a random matrix with the same share of ones. Each simulated person is knocked at four sites, and the highest value is kept, as PCImax was in the benchmark.

x   = tanh(r @ W.T * g + noise + pulse_at_t0)
off = rises towards adapt * max(x - 0.3, 0), else decays (tau 20 steps)
r   = x * (1 - off)          # what other nodes receive
y   = r - 0.9 * off          # what the electrode records

B   = |mean_over_trials(y) - baseline| > 1.15 * max_baseline_deviation
B   = keep runs of 2 or more significant samples
PCI = LZ76(B ordered by activity, read time-major) * log2(L) / (L * H(p))

The output

I ran seven benchmark conditions with twelve simulated people in each, then four simulated patient groups, and the conditions differ only in the settings of the three knobs. Wake and ketamine have high gain and no adaptation, with extra noise for ketamine. REM sleep has light adaptation, while NREM sleep, propofol, xenon and midazolam have heavy adaptation and, for the drugs, lower gain.

$ python3 instrument.py   # seed 40, 12 simulated subjects per condition, max PCI over 4 sites
wake       median 0.589 range 0.526-0.646
ketamine   median 0.581 range 0.529-0.640
REM        median 0.425 range 0.366-0.549
NREM       median 0.109 range 0.086-0.123
propofol   median 0.116 range 0.101-0.135
xenon      median 0.173 range 0.147-0.280
midazolam  median 0.121 range 0.104-0.138
cutoff 0.28 auc 1.0 sens 1.0 spec 1.0
MCS             median 0.288 range 0.177-0.299 above 7/12
VS low          median 0.093 range 0.082-0.119 above 0/12
VS high         median 0.530 range 0.409-0.591 above 12/12
VS no-response  median 0.000 range 0.000-0.000 above 0/12

The toy reproduces the overall shape of the clinical benchmark. Wake, ketamine and REM sit well above the rest, and a cutoff of 0.28 separates them perfectly. That cutoff happens to be close to the real 0.31, but this is partly luck, since the absolute values depend on my analysis choices. The simulated patient groups also fall where their settings put them. Simulated patients with injured links but no bistability score like waking people, and those with heavy bistability score like sleepers.

The simulated MCS group is the weakest point of the comparison, because its median of 0.288 sits just above the toy cutoff, and only seven of twelve clear it. In the real data, 36 of 38 MCS patients cleared the line. My MCS knobs, moderate injury with moderate bistability, sit near the crossing point of the model, so small changes tip them either way. That is a real limitation of the toy, and it may also be a hint that MCS is a borderline state in more than the clinical sense.

Bistability is enough

The first claim was that bistability alone can collapse the echo, so I held gain fixed at waking levels and increased adaptation in steps. The output crosses the cutoff between adaptation of 0.3 and 0.4, and by 0.6 the toy cortex scores like a sleeper. Nothing else changed: the connections were identical and the gain was identical. In the toy, a cortex with every wire intact gives a sleeper’s score once its nodes start falling silent after each burst.

$ python3 sweep.py   # seed 410: [adaptation, median PCImax, min, max], gain fixed at 0.97
adapt [0, 0.585, 0.484, 0.676]
adapt [0.1, 0.612, 0.526, 0.638]
adapt [0.2, 0.468, 0.367, 0.573]
adapt [0.3, 0.335, 0.298, 0.417]
adapt [0.4, 0.228, 0.21, 0.298]
adapt [0.5, 0.169, 0.151, 0.22]
adapt [0.6, 0.123, 0.109, 0.139]
adapt [0.8, 0.111, 0.099, 0.123]
adapt [1.0, 0.108, 0.089, 0.127]

I then combined every level of long-range strength with every level of adaptation in a grid. With no bistability, cutting 80% of long-range links barely changed the score, from 0.569 to 0.538. With moderate bistability, the same cut lowered it from 0.391 to 0.218. With heavy bistability, the links did not matter, because the score was already at the floor. The two knobs interact, and the toy suggests that injury and bistability together are worse than either alone.

Kabir’s injury is diffuse damage to white matter, which is the long-range knob. The grid says that if his surviving cortex is not bistable, his PCI could be high even with many links lost. If his cortex has become bistable, as Rosanova and colleagues found in most UWS patients, the same injury would push him down. The toy cannot tell us which description is true of Kabir, although it does tell us what the number would be tracking.

Where the argument fails

Three parameter sweeps show where the single number becomes fragile. The first varies the number of trials averaged: with 10 trials, the toy waking median was 0.678, and with 400 it was 0.482, and NREM also fell, from 0.145 to 0.084. The gap between the states held at every trial count, but the absolute values drifted by about 0.2. A fixed cutoff assumes a fixed protocol, which is exactly what Casarotto and colleagues warned.

$ python3 sweep.py   # seed 420: [trials, wake median, wake min, NREM median, NREM max]
trials [10, 0.678, 0.565, 0.145, 0.213]
trials [20, 0.72, 0.545, 0.127, 0.167]
trials [40, 0.655, 0.545, 0.109, 0.154]
trials [80, 0.603, 0.483, 0.095, 0.106]
trials [200, 0.53, 0.458, 0.1, 0.123]
trials [400, 0.482, 0.44, 0.084, 0.117]

The second sweep changed the threshold for keeping a deflection, from 1.0 to 2.4 times the largest baseline deviation. The waking values moved only between 0.525 and 0.572, and NREM between 0.084 and 0.107. In this toy, the significance threshold was considerably less fragile than the trial count.

The third test was an island of preserved activity. I made four of the six modules bistable and left two awake, as if a patient had preserved cortex in one region only. Knocking the bistable modules gave 0.084 and 0.056, while knocking the awake ones gave 0.563 and 0.593. A protocol that stimulates only damaged cortex would miss a working island entirely. This is the reason the benchmark uses several sites and keeps the maximum, and it is why lesion maps matter in choosing where to knock.

What the toy leaves out

The simulation omits almost everything that makes real measurement difficult. It has no skull, no scalp, no muscle artefacts and no auditory or somatosensory responses to the coil. Its electrodes record each node directly, whereas real EEG mixes signals from many sources and requires mathematical reconstruction. Its anatomy is a random modular graph rather than a thalamocortical system with layered cortex, and its bistability is a single adaptation variable rather than the interplay of ion channels, neuromodulators and thalamic rhythms described in sleep physiology.

Those omissions cut in a particular direction, because every source of contamination missing from the toy would, in a real recording, add structure that is unrelated to the cortical interactions PCI is meant to capture. The toy therefore shows the measure working under unusually favourable conditions. If the index is fragile here, with respect to trials, sites and nearly empty matrices, it is unlikely to be less fragile in a hospital.

The instrument leaves both claims standing, with explicit conditions attached. Bistability alone is enough to collapse the toy echo, which fits the mechanism in Part three. The single number is fragile to the protocol and the site, which fits the authors’ own warnings. The toy says nothing about experience, and it shows only what a knock-and-listen measure can and cannot see in a system whose rules we wrote.