Designing a Causal Circuit Experiment

Illuminate the dorsal striatum of a mouse that carries no opsin at all, and its firing rate falls and it starts turning to one side. Owen, Liu and Kreitzer reported that in 2019, in vivo and ex vivo, in wild-type animals. If light alone can do that, then your light-on versus light-off comparison was never a comparison between activity and no activity. It was a comparison between light and no light, in animals that happened to express an opsin.

This lesson is about the gap between those two statements, and about the rest of what keeps a causal claim honest: which controls, which sample size, which experimental unit, and how far a human imaging association can be pushed.

The idea: a manipulation answers what a recording cannot

Most of this course has rested on measurement. A recording, an imaging signal or a lesion association tells you that activity goes with a behaviour. None of them tells you whether the activity produces it. The attention and decisions lesson gives a case: choice-related activity in LIP that reversible inactivation showed was not needed for the choice under the conditions tested.

Changing the activity on purpose tests the causal question, and it splits into two questions that are easy to confuse.

A gain-of-function manipulation drives the activity and asks whether it is sufficient to produce a specified behavioural change under the tested conditions. A loss-of-function manipulation suppresses the activity and asks whether it is necessary for that behaviour under the same conditions. Both conclusions are narrow by construction: they hold for the cells you targeted, the time window you illuminated and the assay you scored. A partial reduction in behaviour when you silence a population is evidence that the population contributes, not that it is required.

The tool that made this routine has two separate histories. In 2003 Nagel, Bamberg and colleagues characterized channelrhodopsin-2 as a directly light-switched, cation-selective channel in Xenopus oocytes and in mammalian cells, and reported that it desensitizes in continuous light to a smaller steady-state conductance. In 2005 Boyden, Zhang, Bamberg, Nagel and Deisseroth expressed it with a lentivirus in cultured rat hippocampal neurons and showed reliable millisecond-timescale control of spiking. That 2005 paper had no animal and no behaviour in it; it was a tool demonstration in a dish. The channel’s gating and ion selectivity belong to ion channels as receptors in the signaling course, and restricting expression to one cell type relies on genetic targeting; for how genes are manipulated at all, see CRISPR and functional genomics.

A usable causal claim names four things: the cells, the projection, the timing and the behaviour. Tye and colleagues did this in 2011 in freely moving mice. Rather than illuminate the basolateral amygdala, which drives all of its outputs at once, they illuminated its terminals in the central amygdala. Activating those terminals acutely reduced anxiety-related behaviour; inhibiting them with eNpHR3.0 increased it. You met those structures in emotion and stress.

Controls that make a light experiment mean something

The minimum design is a two-by-two: construct crossed with light. Opsin plus light, opsin without light, fluorophore-only plus light, fluorophore-only without light. The quantity you care about is the interaction, the extra effect of light in animals that carry the opsin. Tye and colleagues included a control-virus group receiving the same illumination parameters, and their stimulation used 5 ms pulses at 20 Hz, which is a 10 percent light-on duty cycle, or 100 ms of light in each second.

Three failure modes of the manipulation deserve checks rather than assumptions. Long channelrhodopsin-driven depolarization can suppress spikes through depolarization block, so driving harder can silence the cell you meant to drive. Anion-conducting silencers can excite neurons when internal chloride is high, as in some axonal compartments. And abruptly ending a period of silencing can produce rebound firing, so the window after the light is part of the result. Each is a reason to validate the physiology in your own preparation, with recordings during and after the light, rather than infer it from the construct’s name.

For a projection claim there is a further problem. Light at a terminal field can also excite axons passing through, and can drive the parent cell bodies, so “I illuminated terminals” is not yet “transmission at this synapse mattered”. Blocking receptors locally at the terminal field is the test that closes that gap: in Tye and colleagues’ mice, blocking glutamate receptors locally in the central amygdala abolished the light-induced reduction in anxiety-related behaviour.

Then the ordinary hygiene, which is where published work most often fails. Verify expression and fibre placement blind to group. Randomize allocation, counterbalance the order of repeated conditions, define exclusions in advance, and score behaviour blind. Add an off-window illumination condition if the claim is about timing, and a locomotor control if a motor explanation is available.

Effect size, power and the experimental unit

Now the arithmetic. The numbers here are invented for teaching.

Suppose a pilot in mice gives a mean avoidance time of 60 s in the opsin-plus-light group and 48 s in the fluorophore-plus-light group, with a pooled standard deviation of 12 s. The standardized mean difference for independent groups is the difference divided by that pooled standard deviation:

d = (60 s − 48 s) / 12 s = 1.0

For 80 percent power at a two-sided alpha of 0.05, the sample size per group for a two-group comparison is:

n per group = 2 (1.96 + 0.84)^2 / d^2

With d = 1.0 that is 2 × 7.84 / 1 = 15.7, so 16 animals per group, or about 17 once you allow for using a t distribution rather than a normal one. Now ask the question a planner must ask: what if the true effect is half the pilot estimate? At d = 0.5 the same formula gives 15.7 / 0.25 = 62.8, so 63 animals per group. A small pilot is a biased estimate of its own effect, because a pilot that happened to overshoot is the one that gets followed up. Power your confirmatory study on the smallest effect you would care about, not on the pilot.

● p < 0.05 ○ not significant ┆ true d ┆ cutoff for p < 0.05 │ mean of followed-up pilots

True effect d 1.00 (standardized difference) Animals per group n 8 (one number per animal)

Resample (200 experiments) Follow up only significant pilots

Fraction with p < 0.05: observed | expected

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Mean observed d among followed-up pilots | expected | true d

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Planning formula at this true d: n per group

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The lesson’s pilot: d = (60 s − 48 s) / 12 s = 1.0, so n per group = 2 (1.96 + 0.84)² / 1.0² = 15.7, which is 16 animals per group (about 17 with a t distribution). At d = 0.5 it is 15.7 / 0.25 = 62.8, so 63 per group.

Press Resample to draw 200 experiments.

In this sketch: normal data, equal and known SD (z test), two-sided α = 0.05, 80% power as the planning target, one number per animal, invented numbers. Expected fraction = Φ(d √(n/2) − 1.96) + Φ(−d √(n/2) − 1.96), derived from the lesson’s formula (the second term is the opposite tail). “Followed up” means significant with the opsin group higher. Eight mice with 40 trials each is n = 8, not 320. The lesson’s correlation arithmetic (n about 780 for r = 0.10) is left to the text.

Rule to keep: power the confirmatory study on the smallest effect you would care about, not on the pilot.

The n in all of this counts experimental units, and reporting guidelines ask you to say what the unit is: an animal, a litter or a cage. If you illuminate eight mice for 40 trials each, you do not have 320 independent observations. You have eight animals with trials nested inside them, and the analysis has to carry that nesting. Inflating the unit is the quickest way to a significant result that will not replicate.

Why small human samples mislead

Human work substitutes a different measurement with different limits. The conventional imaging signal indexes blood-oxygenation changes associated with neural activity, not spikes. In monkey visual cortex, Logothetis and colleagues recorded electrically and with that signal at the same time and found that local field potentials estimated it better than multi-unit activity did, which led them to suggest that it reflects input and intracortical processing rather than spiking output. For recording the activity of many neurons directly, see recording many neurons.

Size and sampling are the second limit. In Marek and colleagues’ rigorously denoised analysis of 3,928 ABCD participants, the median absolute univariate brain-wide association with behaviour was 0.01, and the largest univariate correlation that replicated out of sample had an absolute value of 0.16. Replication rates improved as samples grew into the thousands, and resampling showed that independent subsamples of 25 people could support opposite conclusions about the same association. Elliott and colleagues, pooling 90 task-fMRI experiments and 1,008 participants, reported a mean test-retest intraclass correlation of 0.397, which matters because an individual-level biomarker needs stable individual rankings, not a strong group average.

Keep the scope. This is about brain-wide association studies of individual differences. It is not a verdict that imaging is unreliable, and it does not set a minimum sample for every within-subject design, where each person is their own comparison. Work on study design since has shown that sampling scheme, and keeping within-person change separate from between-person differences, change the effect sizes you can detect at a given sample size.

Here is the precision calculation to run before trusting an association. Suppose the true correlation is 0.10, which is the order of magnitude Marek and colleagues report. Using the Fisher transformation (atanh, the inverse hyperbolic tangent), the sample size needed for 80 percent power at a two-sided alpha of 0.05 is:

n = (2.80 / atanh r)^2 + 3 = (2.80 / 0.1003)^2 + 3 = about 780

Compare what a study of 25 people can say. The standard error of the transformed correlation is 1 divided by the square root of n minus 3, which is 1 / sqrt(22) = 0.213. An observed correlation of 0.10 then has a 95 percent interval on the transformed scale of 0.100 ± 1.96 × 0.213, from −0.318 to +0.518, which converts back to correlations from about −0.31 to +0.48. The sign is unknown. That is the arithmetic behind two subsamples of 25 disagreeing.

Design problem

A paper reports the following. Twenty patients and twenty controls are scanned. The authors search all connections and all symptom measures, pick the strongest symptom-connectivity relationship, and report cross-validated prediction after splitting each person’s two scans across different folds. They name a mouse projection as the cause of the disorder, then activate that projection with light, comparing light-on with light-off in opsin-expressing animals, scoring avoidance unblinded, and counting each trial as a replicate. Their discussion proposes stimulating the human homologue as a treatment. Rewrite the study.

One way to do it

Start by separating three claims the paper runs together: an association in humans, a prediction target, and a causal intervention in mice. A cross-sectional scan plus an acute mouse assay licenses no statement about the mechanism of a human disorder.

On the human side: prespecify the imaging target, or validate it in an independent sample. Do feature selection and model tuning inside the training folds only, since choosing the strongest relationship from all the data and then cross-validating it reports a number that has already seen the answer. Split by person, never by scan, so no participant appears in both training and evaluation. Report the effect size and its uncertainty rather than a p value, and measure the test-retest reliability of the specific variable you propose as a marker. Forty participants cannot resolve an association of the size this literature reports, so either join a large cohort or reframe the study as a within-person design. Check the alternatives that diagnosis is confounded with: medication, head motion, and how the two groups were recruited.

On the mouse side: add the opsin-negative arm and make the contrast light-by-construct, because light alone changes firing and behaviour. Verify expression and fibre placement blind, and verify the physiology during and after illumination, including the offset. Run both arms, activation for sufficiency and silencing for necessity, in the same prespecified window. If the claim is projection-specific, block transmission locally at the terminal field. Randomize allocation, blind the scoring, define exclusions in advance, and analyze trials nested within animals with the animal as the unit.

Then write the conclusion the design supports: replicated, controlled evidence that activity in a named projection contributes to an assay-defined behaviour in mice during a defined window, alongside a separately reported human association with its uncertainty and reliability. A therapeutic claim would need human interventional evidence, which this study does not contain.