10: What Does One Attachment Cause?

The last chapter took away the body’s privilege.

Two attempts to identify a privileged boundary around the connected occupied crystal both failed. What survived was narrower and more useful: local interventions produced spatially localized consequences under the tested protocol.

So stop drawing the object first.

Start with an event. That is a statement about events and their effects rather than about objects and their edges, and it suggested we had been starting at the wrong end of the problem.

So start at the other end. One event. What does it do?

That question turns out to conceal several different causal claims.

The chapter is the process of forcing them apart.

Does the Process Move?

The first instinct, having lost the body, is to look for something else with an outline. If the connected body is not the right experimental object, perhaps the activity itself has spatial organization — something that moves through the interface and generates structure as it goes.

That is testable. If activity genuinely propagates, then activity near one location at time t should predict activity farther away at later times, in a structured way:

near distance  →  early lag
far distance   →  later lag

A moving ridge through space and time.

So we built an event field out of material-changing events, measured future event density at each distance and lag from each event, and compared it against matched non-event locations sharing local geometric context — plus a cross-run control, since ordinary developmental progression could manufacture a distance-lag trend without anything travelling at all. The primary statistic asked whether the lag holding the excess activity shifted outward as distance increased.

It did not shift enough. The paired test missed its frozen gate, and the propagation claim failed.

Two secondary shape statistics nevertheless looked suggestive. Distance and estimated ridge lag were positively associated.

That made the surface worth inspecting directly rather than promoting a failed primary result.

Then we looked at the surface itself.

The Estimator Invents a Wave

At distance one, the real event field had a small positive excess at the first lag and negative excess afterwards. The statistic weighted positive values only, so its centroid collapsed onto lag one.

At larger distances there was no real structure — just weak noise scattered across the lag grid. Weight noise positively and average it and you get a centroid somewhere in the middle of the grid.

Put those two facts together and the estimator reports:

distance 1     →  early lag
far distances  →  middle lags

which is exactly the shape of a ridge moving outward. There was no ridge. There was one strongly anchored near-distance row and a field of noise, and the measurement device turned that into apparent motion.

The danger is obvious in retrospect. A statistic designed to summarize a travelling ridge produced the expected shape even when the underlying surface contained no travelling ridge.

A positive result on that statistic could therefore have become a result about the estimator rather than the Crystal.

An estimator can manufacture the shape of the phenomenon it was designed to detect.

There is a second lesson buried in the same failure. The strongest structure in the surface was not positive at all. It was a persistent negative band at short range.

The positive-only estimator had discarded it before inference began.

So the instrument had made two mistakes at once:

noise acquired the shape we were looking for

real signed structure was removed because it had the wrong sign

So we closed the propagation claim, kept the signed structure the estimator had been suppressing, and looked at it directly.

Look at the Signs Instead

Separating events by type and keeping the sign gives a much simpler picture — but only after removing a confound sitting at the origin.

At distance zero, a source and its control are definitionally different states. An attachment source is occupied where its control is empty; a loss source is empty where its control is occupied. Those differences mechanically determine what can happen at that same site later. They are not neighbourhood dynamics at all, and including them contaminates everything.

Exclude distance zero and the neighbourhood result comes out clean. At distances one and two:

ATTACHMENT  →  MORE nearby attachment
LOSS        →  LESS nearby attachment

with the strongest signed structure concentrated at the shortest tested neighbourhood distances.

That is the wrong sign for the simple source/sink interpretation we had been carrying.

But it is exactly the sign predicted by the ordinary local attachment rule.

The Rule Already Predicts This

The attachment rule rewards occupied neighbours. That term is positive. So:

x attaches
↓
nearby empty cells gain an occupied neighbour
↓
their attachment probability rises

and symmetrically, a cell disappearing lowers the probabilities around it.

The observation is precisely what the rule says should happen. Which is almost embarrassing as a discovery, and exactly why it needs an intervention rather than an observation.

Because the observational version has a serious confound: the sites that actually attached were not randomly chosen. They attached because they were probable, which means they already sat in favourable local geometry, which means their neighbourhoods may have been on their way somewhere regardless. Correlating what happened after real attachments with what happened after matched non-attachments cannot fully separate the attachment’s effect from the conditions that produced it.

So stop watching. Intervene.

Force One Attachment

Take a checkpoint. Take one eligible frontier cell x. Take the same environment and the same cell-keyed randomness from Chapter 5. Then split the future:

FORCE      x attaches
PREVENT    x does not attach

and measure everything except x itself.

That exclusion is the whole design. We are not asking whether two states that differ at x still differ at x later — that is trivially true and tells us nothing. We are asking what happens around x because the state at x was changed.

One more thing before looking at any outcome: calculate what the frozen rule mechanically predicts the immediate effect should be. Every candidate near x has an attachment probability in each branch, and those probabilities can be summed before any random draw is taken. Call the expected one-step difference g_mech_1, and the realized neighbouring difference g1.

This matters more than it sounds. Almost every experiment in this book has compared a measurement against zero. Here the mechanism already predicts a specific nonzero value, so zero is the wrong benchmark. The real question is not did something happen but did what happened match what the rule says should happen.

The First Effect Is Mechanical

mechanically expected one-step gain     g_mech_1 ≈ 0.105
realized one-step neighbouring gain     g1       ≈ 0.115

The discrepancy interval included zero and stayed inside the frozen accounting tolerance. A later fresh-seed experiment replicated it:

g_mech_1        0.0883    [0.0676, 0.1095]
g1              0.1016    [0.0677, 0.1380]
g1 − g_mech_1   0.0132    [−0.0160, 0.0411]

CONSISTENT WITH MECHANICS

Forcing one eligible frontier attachment causes additional neighbouring construction on the next update, at a magnitude consistent with the frozen local attachment rule.

This is an unusually clean causal result.

We have a controlled intervention, a fresh-seed replication, and an immediate effect whose measured magnitude is consistent with the effect predicted by the frozen rule.

The result is valuable precisely because no additional one-step amplification needs to be invoked to explain it.

Everything that follows is about what happens after the first update, where the accounting stops being easy.

Then the Futures Keep Separating

Ten updates after the intervention, the cumulative construction difference was around:

G_10 ≈ 0.58

Only a small fraction of that appeared in the first step. The branches kept diverging, update after update, and it was tempting to read that as a cascade — one attachment causing others, which cause others, the perturbation feeding itself forward through the crystal.

It was also tempting to compare 0.58 against the obvious reference value of one additional event per initiating event, note that it sits below, and start reaching for vocabulary about branching and subcriticality.

But there is a confound sitting in the middle of the design, and it is the same shape as the confound that ruined the surface-versus-interior comparison in Chapter 6.

In the FORCE branch, x is still there. It did not merely happen; it remains occupied, and it goes on being an occupied neighbour to everything around it on every subsequent update. So the accumulating difference could be either of two quite different things:

a free-running cascade
    the consequence propagating on its own

or

the continuing consequence
    of one cell being permanently different

Those are not the same phenomenon, and the experiment as built could not tell them apart.

Remove the Cause

The fix is a third branch.

PREVENT      x does not attach

PERSISTENT   x is forced to attach, then remains under normal dynamics

TRANSIENT    x is forced to attach, gets one full causal update,
             and is then removed

The transient arm is the critical control.

It allows the forced attachment to influence one complete subsequent update. Then the initiating occupancy difference is removed.

From that point onward, any remaining divergence has to be carried by consequences already created downstream rather than by the continued presence of x.

Can a causal consequence sustain itself after the material difference that started it is gone?

That is a far better question than asking whether FORCE and PREVENT still differ later. It also required a correction to the intervention timing: force and prevent now happen inside the canonical growth update, with the ordinary loss step applied to every branch afterwards, so that the forced cell faces the same background loss as any other newly attached cell.

The fresh-seed run used 96 independent groups and 384 interventions across four predeclared frontier-probability strata, with the observation window extended to thirty updates.

The Cascade Runs Out

G_transient(30)   0.198    [−0.026, 0.440]

More informative than the total is the late-time rate. Across updates 21 through 30:

transient late gain   −0.0081 per update    [−0.0201, 0.0039]

which passed the frozen practical-convergence criterion. Within the tested late window, the transient branch shows no continuing positive accumulation rate.

The downstream residue has converged under the predeclared criterion.

Once the initiating occupancy is removed, the remaining causal cascade is small and exhausts itself over the tested horizon.

The thirty-update transient total also sits below the descriptive reference value of one, and it is worth stating plainly what we are not saying. This is not a branching ratio. We have not established subcriticality, criticality, or any position relative to a phase transition. Those terms come from theories with structure this experiment has not tested — a branching ratio presumes a well-defined offspring distribution, and we have measured a construction difference under one intervention, one horizon and one substrate. The number is below one. That is all it means.

Leave the Cause in Place

The persistent arm behaves very differently.

G_persistent(30)                  1.164    [0.786, 1.542]
G_transient(30)                   0.198
difference                        0.966    [0.612, 1.333]

The thirty-step consequence is substantially larger when the initiating state difference remains present than when it is removed after one causal update.

PERSISTENT STATE DIFFERENCE
≠
TRANSIENT CAUSAL CASCADE

This is the same lesson Chapter 6 taught about material traces, arriving now at the scale of a single cell. There, persistent material mattered while it stayed coupled to the interface, and the persistence was doing the work rather than any propagating consequence. Here, the continued state difference carries substantially more cumulative consequence than the transient residue left after that difference is removed.

But persistent does not mean permanent, and the obvious next interpretation dies too. If keeping x gave the branch a standing growth advantage, cumulative gain would rise roughly linearly with horizon forever. It does not:

H=1     0.156
H=5     0.539
H=10    0.839
H=17    1.008
H=22    1.190
H=30    1.164

and the late-window rate was:

persistent late gain   0.0057 per update    [−0.0159, 0.0281]

An interval spanning zero, far below the predeclared offset threshold. The persistent trajectory rises early, flattens, and then wanders. No permanent positive growth offset was established.

So under this intervention and horizon, one attachment produces:

an immediate mechanically accounted effect
↓
a small downstream residue
↓
a larger finite consequence if the initiating state persists

Four Different Claims

It is worth separating what has now become four distinct causal statements, because ordinary language collapses them into “the attachment mattered”:

DIRECT MECHANICAL EFFECT          measured, and accounted for by the rule
TRANSIENT DOWNSTREAM CASCADE      measured, small, convergent
CONSEQUENCE OF PERSISTENT STATE   measured, substantially larger, finite
PERMANENT GROWTH-RATE CHANGE      not established

Only the first three have evidence. They are not interchangeable, and an experiment that measures one and reports another — which is what the ten-update version was doing — will get the story wrong in a way no amount of extra precision would fix.

The Same Event Means Different Things in Different Places

One more result from the intervention runs, and it is the one that generates the second half of the chapter.

The four probability strata sit in visibly different geometry. The lowest-probability probes were sparse sites — mean baseline attachment probability around 0.372, with almost exactly one occupied neighbour. The highest-probability probes were dense — baseline around 0.798, with roughly 4.07 occupied neighbours.

Force an attachment at each and the immediate effect on frontier opportunity changes sign with local geometry.

                            SPARSE      DENSE

newly promoted frontier      2.23        0.031
total frontier change       +1.23       −0.969

At a sparse interface, occupying one cell gives several previously unsupported empty neighbours their first occupied neighbour, and new frontier appears. At a dense interface, almost everything nearby is already occupied or already eligible, so the only substantial change is that the focal site itself leaves the frontier — the attachment consumes opportunity rather than creating it.

The paired difference in frontier creation was about 2.20 sites, interval [1.99, 2.41], p = 0.000125.

The same one-cell attachment can create or consume very different amounts of future construction opportunity depending on local geometry.

That is solidly established, and it immediately suggests something stronger.

But Geometry Did Not Predict Long-Run Gain

The obvious stronger hypothesis is that sites creating more immediate frontier opportunity should also produce larger downstream causal consequences.

The point estimates encourage it:

sparse probe    G_transient(30) ≈ 0.677
dense probe     G_transient(30) ≈ 0.073

The predeclared paired comparison does not:

difference   0.604    [−0.031, 1.271]    p = 0.0777

and the persistent-arm version is worse still (difference 0.156, p = 0.810).

So we have established that sparse and dense geometry differ, and we have not established that sparse geometry produces reliably higher long-run gain. The point estimates make the relationship interesting. They do not make it true.

Surely We Can Map Causal Gain

The immediate geometric contrast is strong enough to motivate a more ambitious hypothesis:

perhaps downstream causal consequence can be predicted from local state before the intervention occurs.

If so, causal leverage might be map-able across the frontier rather than measured only after the fact.

Which is a genuinely attractive hypothesis. If it held, the crystal would contain a causal field: a map assigning each frontier site a leverage value, high in some places and low in others, derivable from local structure. That would be a substantial discovery — the first quantity in this book that a location could be said to have.

The natural candidate is the geometric one:

FCP(x) = |frontier after forcing x occupied| − |frontier before|

Frontier Creation Potential — positive when occupying x creates net opportunity, negative when it consumes it. An observer-defined quantity, not energy, not fitness, nothing hidden. And the hypothesis writes itself:

Sites that create more frontier opportunity produce more transient causal gain.

Three Attempts, and What They Could Actually Resolve

The first FCP experiment looked promising and could not answer the question. With 48 groups, the high-minus-low transient gain came out at:

+0.167    [−0.078, +0.431]

against a declared meaningful effect of +0.15. An interval that wide cannot distinguish an effect at that scale from nothing, in either direction. That is not a failed hypothesis; it is an experiment without the precision to test the hypothesis it declared. The distinction matters enormously, and reporting it as a negative result would have been a straightforward misrepresentation.

A missed significance gate is not a negative result unless the experiment could have resolved the effect it said mattered.

The second attempt asked whether FCP was simply too compressed a description. A frontier cell on the hexagonal lattice has six neighbours, each occupied or empty, so the exact ring is six bits. Perhaps the precise arrangement matters in ways a scalar count destroys. That experiment was even less precise — a primary interval half-width around 0.50 attachments against a declared effect of 0.20. Inconclusive again.

It did expose a design problem worth keeping. The comparison matched tightly on baseline attachment probability, but the frozen rule computes attachment probability from local exposure geometry. Conditioning on it holds fixed one of the main pathways through which geometry could act, converting a broad question into a narrow one about residual effects. A control is not automatically conservative.

If it conditions on a variable lying on the causal pathway under investigation, it can remove part of the mechanism the experiment was supposed to measure.

The third attempt moved from geometry to process history. Two sites can look identical now and have arrived there through very different recent activity, so this compared high and low recent turnover while matching present local state. The manipulation was large — about 7.73 events of difference — and the transient-gain difference was:

−0.065    [−0.221, +0.096]

whose positive side genuinely excludes the declared +0.15.

But the scope of that result is narrower than it looks, and the reason is structural. Persistent material modification was disabled in that substrate, so the operative dynamics were determined by current occupancy, current input and keyed randomness. Past turnover could only influence the future through the present state it had already produced — and the present state was exactly what the matching held fixed. That experiment asked whether recent turnover proxies for present information the matching missed. It is not a test of whether history can matter in a substrate built to carry it.

Stop Searching Features

At this point the path forward is obvious and wrong. Bigger motifs. A longer history window. A learned predictor over some richer feature set. Keep going until something correlates with gain.

That procedure has no stopping rule and produces no knowledge, and we have declined it twice already — after the placement experiments in Chapter 6 and the budget experiments in Chapter 8. So instead of another feature, rebuild the measurement.

The reset kept the frozen crystal and the FORCE/PREVENT intervention and changed what was measured. Rather than starting from the noisy realized cascade, start from the rule: for every candidate, compute the attachment probability in each branch and take the difference, before any Bernoulli draw turns those probabilities into a single bit. A realized attachment discards almost all the information the rule provides; the expected construction difference keeps it.

The contrast was made extreme — high sites with FCP ≥ +2, low sites with FCP ≤ −1, every pair differing by at least 3 — matched on occupied-neighbour count and radial band, and deliberately not matched on baseline probability or local frontier density, since those lie on the pathway. It ran 384 groups and yielded 275 usable ones, 471 extreme pairs, 71.6% coverage.

This time the precision was adequate: an achieved minimum detectable effect around 0.047 against a declared meaningful effect of +0.10. And the result was:

ΔE1 = −0.0026    [−0.0395, +0.0333]

Under this protocol, even an extreme difference in Frontier Creation Potential did not produce the predeclared scientifically meaningful positive difference in expected lag-one local construction.

That is a bounded negative, not another inconclusive run. The bounded claim is now properly resolved:

MORE FRONTIER CREATION
↛
MEANINGFULLY MORE EXPECTED
LAG-ONE LOCAL CONSTRUCTION

A Causal Effect Without a Stable Local Predictor

Put the two halves of the chapter together.

A local intervention has a real causal future. Its immediate effect is measurable, replicated, and quantitatively explained by the rule. Its transient cascade is small and self-exhausting. Its persistent-state consequence is several times larger and still finite. And the same intervention transforms future opportunity in dramatically different ways depending on where it lands.

What we could not establish was a stable local predictor of downstream consequence.

Three candidate descriptions were tested:

Frontier Creation Potential
exact local motif
recent local history

Be precise about what that licenses. We did not show that downstream consequence is unpredictable. We showed that three specific representations either lacked the precision to answer or, in the one properly powered case, did not predict. Better predictors may exist.

But the word gain has been quietly doing damage, and it is worth saying so. It invites a picture in which each site holds a stored quantity — this cell has gain 0.8, that one 0.2 — waiting to be released. That is the picture behind linear-response thinking generally, where a system’s reaction is characterized by a response function belonging to the point you poke. The measurements do not support it here. What we have instead is:

intervention
↓
changes local occupancy
↓
changes which opportunities exist
↓
changes what gets evaluated
↓
changes some attachments
↓
changes later opportunities
↓
the difference dissipates, or goes somewhere

This makes an interaction-generated account plausible: the consequence may depend on what the intervention changes in the subsequent process rather than on a scalar property stored at the intervention site.

That is an interpretation to test, not yet a demonstrated mechanism. The analogy is useful if kept narrow: asking where the causal consequence is stored beforehand may be like asking where a traffic jam is stored before the interacting traffic produces it.

The safest version of the chapter’s conclusion, and the one fully earned:

We found a causal effect before we found a stable local variable that predicts its downstream size.

Evidence Ledger

Where Does the Difference Go?

There is one measurement left over, and it does not fit anywhere in this chapter.

Throughout the intervention runs we tracked causal gain twice: locally, around the intervention, and globally, across the whole crystal excluding the intervention site. For the persistent arm those measurements were approximately 1.164 locally and 1.036 globally. For the transient arm they were approximately 0.198 and 0.044.

Their differences have intervals spanning zero.

So there is no established far-field causal effect here.

But the unresolved discrepancy points directly at a mechanism the local experiments have not yet isolated. The selected candidate sets remained more than 99% overlapping between branches.

So any scheduling-mediated effect, if one exists, is subtle rather than a wholesale rewriting of the global evaluation schedule.

But the sign is worth sitting with. If a local intervention only helped, the global gain should be at least as large as the local gain. It is smaller. Something looks like it is being taken from elsewhere, and the reason it might be is not mysterious at all: Chapter 8 gave every active location in this substrate something it shares with every other active location, a finite pool of evaluation opportunity. And the one thing this chapter has established beyond argument is that a local attachment changes the frontier — sometimes by two sites, sometimes by minus one.

Change the frontier and you change the candidate population competing for a fixed evaluation budget.

That creates a concrete route by which a local intervention could affect distant opportunities without any local causal chain connecting the two sites.

That possibility has not yet been tested directly.

Chapter 9 failed to find a privileged enclosing body.

This chapter found a local causal effect but no stable local gain variable that predicts its downstream size.

Both now point toward the same untested mechanism: the finite evaluation budget shared by every active candidate.

Can finite computation couple local events that are too far apart to interact through the local rule?