"Stereotyped position of local synaptic targets in neocortex"

This is the title of a recent paper in Science (James Kozloski, Farid Hamzi-Sichani, Rafael Yuste, Science, Vol. 293, P.868). In the abstract the authors go even further, and the last two sentences say: "Moreover, even the position of the followers appeared determined across animals. Our data reveal precisely organized cortical microcircuits." If this is true, that would seem to contradict what I write about stochastic connectivity, so here is an in-depth review of this paper.

The first standing out feature of the paper is that all the spatial analysis in this paper is done in a plane perpendicular to the plane of the cortex (see Figure 2). The location along the Medial-Lateral axis is all the information about in-plane position. In other words, all the directions inside the plane of the cortex are reduced to two directions.

Why didn't the authors show us data about in-plane relative positions? Here are mail messages from the author explaining the omission. The method they used allows them to see at most 75uM in the direction normal to the plane of the slice, so they decided to "flatten" the analysis, i.e. ignore this dimension and regard everything as if it is on the surface of the slice. This "flattening" may be justified by the difficulty associated with doing better analysis, but, since it eliminates any information about direction inside the cortex plane, it means that the analysis doesn't actually tell us much about the pattern of connectivity of neurons.

While the "flattening" may be justified, it should have been explained in the article, because it makes a large difference to what the data can tell us. In his second e-mail the author points to refs 26 and 27 in the paper, but these do not explain the limitation of the method and the "flattening". He also says that figures 2a-c should make it clear that they observe the surface of a slice, but that would be true only for a very alert reader, which carefully inspects the figure (and even such reader won't be able to understand why it is only a surface of a slice without the additional explanation in the e-mail, or already knowing about the method). Most readers will not pay much attention to the details of the figure, and hence will get a completely false impression of what the results are. Where only the abstract is available (e.g. here) the readers obviously cannot figure out that the data completely ignores directions inside the cortex plane.

On the other hand, the paper repeatedly pushes the idea that it shows "precise organized cortical microcircuits."

1. On page 869 the authors say: "Putative contacts occurred primarily on secondary and tertiary dendritic branches at a characteristic distance from the somata (74+/-36 uM, n=40; Fig 4A, Yellow circle)." i.e. the spread of the distances is far larger than the average distance (only 2/3 of the distances are within 2 s.d. (72uM), the other third are outside this range), yet the authors call this "characteristic distance"! They clearly rely on the reader to skip the numbers.
2. Again on p. 869:"In numerous ways, trigger-follower connections appeared specific and stereotyped from animal to animal. Pyramidal followers were different from CT cells: Their apical dendrites were thinner (1.53 +0.31 uM, n=6; t test P<0.001) and had fewer collateral branches (2.2 +2.1 SD, n=6; t test P<<0.001)." That is, however all that they can say about the pyramidal followers, i.e. they are "specific and stereotyped" in "numerous ways" only in the sense that they differ from the CT cells (which is what we should expect as most pyramidal cells are not CT cells).
3. In the same paragraph the authors prove that the interneurons (non-pyramidal) followers were not randomly drawn from the layer 5 interneurons. This is ridiculous, as the procedure they used to pick up the neurons is clearly not random. It introduces biases, some of which corresponds to real data and some to artifacts of the procedure, and the problem is to distinguish between these biases. The analysis that the authors perform cannot help us distinguish between these biases, and hence is totally irrelevant.
4. The authors continue on p.870 to say that: "furthermore, cluster analysis independently showed that interneurons followers represent only a few of the different types of layer 5 interneurons (see Web fig. 2B)(35)." Quite amusing statement, considering that according to them (p. 868) "the number of different classes of neocortical neurons is still unknown and could approach several hundreds (24)" and that they have only 10 followers interneurons, so clearly the followers could come only from few classes.
5. Next on p.870 the authors start to discuss the position of the followers. As mentioned above, they omit directions inside the cortex plane (reduce them to the Medial-lateral axis) without saying it. What they do say is: "Although triggers were located at a restricted subpial depth, the locations of the three major classes of followers relative to their triggers appeared precisely determined (Fig. 2, D and E), with variances much smaller than that of the depths of the triggers." That sentence is bizarre: (a) the "although" in the beginning implies that the first part should make the rest of the sentence surprising, but it doesn't, (b) it compares the variances in distances to the variances in depths of the triggers, without any hint of an explanation why this comparison is useful (it would be if the variances in depth affect the variances in distances, but there is no reason why this should be the case). These bizarre comparisons are required to establish the "precisely determined" claim.
6. The "precisely determined" is ridiculous even when the directions in the cortex plane are ignored. The authors say: "fusiform followers were always located below and at a distance ~50 uM (51.2 +/12.2 uM, n= 6) from triggers, forming a semi-circle (Fig2, C to E). Meanwhile, triangular followers were located ~65 uM above triggers (66.2 +/ 9.5 uM, n=3)." Thus the variances in the distances of the non-pyramidal cells are pretty large (SD 15% for 3 of them and 24% for 6 of them), and the authors don't bother to tell us the average and SD for the pyramidal cells, clearly because their spread (see fig 2D) is far too large to their taste. The directions in the plane they do show also vary considerably, but the authors don't give any information about these. The statement that fusiform followers "forming a semi-circle" is clearly wishful thinking, as Fig 2.c shows clearly that they don't.

In the data in Fig. 2, the only interesting observation is the vertical stratification of different types, and even this is not "precise" by any sense of the word ("stereotyped" may be justified). The authors then go on to present some statistics they did to test the "positional stereotypy of followers", but the most these tests can establish is the stratification by cell types.

7. In the summary the authors say:" Although our results could be influenced by many experimental factors, they can reveal stereotyped circuits only if they indeed exist." That is simply wishful thinking. There is no problem for experimental factors to generate "stereotyped circuits". For example, the authors put emphasis on the restricted types of the follower neurons (e.g. in the following sentence), but that may be because their method make these types of cells easier to activate than other cell types, and clearly their "flattening" generates "stereotypy" by removing variability.
8. The last sentence of the paper is: "Moreover, even the positions of these targeted neurons appeared determined in different animals and was remarkably precise, indicating robust developmental control of circuit formation." Again repeating the "precise positioning", ignoring direction in the cortex plane and the large variability that is seen even after the "flattening".

Other potential problems with the paper that the authors gloss over are:

1. The number of neurons in the analysis is very small, presumably because the analysis is very difficult, but it still means that the results are unreliable. The small number is obvious to anybody that reads the paper, but not to somebody that reads only the abstract.
2. Normally single neurons in the cortex are not likely to be able to activate other neurons on their own. To actually get their results, the authors needed to 'encourage' them by using a solution that "strengthened synaptic transmission", i.e. the neurons are in a very different environment from their natural one. Again the method is justified, but it makes the results unreliable.
3. The authors actually find as followers only the neurons that are most affected by activity of the target neuron. The vast majority of connections from the target neurons will be to other neurons that are less affected. It is not obvious that there is a good correlation between the distribution of the neurons that are most affected by the target neurons and the rest of the neurons that receive input from it.

In short, while the paper shows some interesting data using a new methodology, it is not even getting close to show "precise microcircuits". The most that it shows is stratification of cell types in the follower neurons. The presentation in the whole paper is very biased and quite misleading, and the abstract on its own is very misleading.

The commentaries that are based on this article are also very misleading. They tend to take the misleading statements, and even exaggerate them, without any critical analysis. The comment in Science itself (p. 759. Science, Vol. 293), for example, claims: "They observed extreme specificity among local synaptic circuit in layer V of the primary visual cortex." So now we have "extreme specificity", which is even more than the paper itself claimed.

The review in Nature Reviews neuroscience of this article gives a good example how already bogus exaggeration in the original paper become completely out-of-touch proclamations in the secondary literature. This review doesn't proclaim "extreme specificity", just "extremely stereotyped local microcircuitry", which is again an "improvement" on the original, which did not have "extremely", but this is not the main "improvement".

The main "improvement" in the review is that it explicitly discusses "specificity at the level of individual neurons". The original paper did not mention this. The review, however, says that:

"Most neurons in the cortex are excitatory, and the rules that govern their local connections are unknown. Perhaps they are interconnected probabilistically, with no specificity at the level of individual neurons. But equally, they might form connections according to strict and intricate rules that we simply have not deciphered yet. A new study by Kozloski et al. suggests that the latter is closer to the truth."

The truthfulness of the "strict and intricate rules" is qualified by "suggests", which makes it even more difficult for the reader to realize that this suggestion is not only divorced from the data in the paper, but even from the interpretations by the authors of the original paper. It is an invention of the reviewer.

The penultimate sentence of the review enforces the point with a nice demagogical trick: "It will be interesting to see whether activity-dependent competition, which is so important in shaping the circuitry of much of the brain, can be reconciled with the apparently rigid way in which these connections are controlled." The reviewer doesn't actually describe how "rigid" are the connections. Instead, she suggests that it will be difficult to reconcile the "rigid way in which these connections are controlled" with "activity-dependent competition", which gives the reader an impression of highly precise connectivity without actually saying it (an example of lying by implication).

The reviewer continues to drive the point in the last sentence: "But a street map of cortical microcircuitry would go a long way towards the formation of realistic theories of cortical function." "Street map" strongly suggests high specificity, with a specific name for each street (neuron), and clearly there is nothing in the paper (the data or the authors' interpretations) that justifies it. This sentence, like the one before, uses implication: it doesn't explicitly claim that the paper suggests that we can find such a specificity that it will make sense to use names for neurons, but it implies it strongly by the fact that it (the sentence) does not make sense otherwise in the current context.

Another point that is worth noting is that the claim by the reviewer in the first paragraph that "Similarly, although the connections between different areas of the cortex, and from neocortex to other brain structures, are well understood,.." is simply false. Even at the level of connections between areas in the cortex there are substantial variations between individuals. This kind of mis-information in the introduction of the review is specially effective, because readers may be somewhat cautious when reading about the new findings, but will tend to assume that what the reviewer claims as background is probably based on well-established facts.

[10 Oct 2001] Just found This page, which really pulls out all the stops. The first sentence already says that the connections are "extremely precise and identical from one individual animal to another." So now we have "identical", which is more than the reviews above dared to claim. The text continues in the same tone, e.g.

"When one neuron was stimulated, a second one, always the same, was triggered."

"Yuste said he was surprised by the identical circuitry among different animals."

The mis-information in this page is so blatant, that readers that read it and also the actual paper may still be confused, and get the impression that the differnt points in Fig 2.c correspond each to neurons from several animals, rather then each of them being a single neuron. Otherwise the "identical circuitry" does not make sense. It is made specially bad by the fact that it is written in cooperation with the senior author of the paper, and therefore looks more authoriative.

The idea that the connections "are identical from one animal to the next" is repeated by the author in other places, e.g. here and here. Since the author obviously knows that this is false, these are straightforward lies.

[ 5 Apr 2003 ] Here (Silberberg, Gupta and Markram, Trends in Neurosciences , Volume 25, Issue 5 , 1 May 2002, Pages 227-230) is a long commentary with the article as the most important reference, by a group that are doing research on the connectivity of the cortex. We first see these statements:

A recent study by Kozloski et al [10] suggests an even greater degree of spatial stereotypy, whereby somata of individual neurons within a microcircuit and precisely positioned relative to each other in a manner that depends on the cell type.

This form of spatial stereotypy.. suggests that each cell lies at a precise point in a crystal-like arrangement of cells, and that the microcircuits comprise multiple such lattices

These authors actually know much better than that. They go on to mention the variability and the small number of neurons (though don't actually mention the numbers, presumably they are too small). They also come out with what they think are arguments that such stereotypy cannot be typical of all the cortex. However, somehow they succeed to keep their belief that the stereotypy exists across animals, and say towrads the end:

Stereotypical microcircuits are a striking feature across different animals of the same species, within exactly the same area at a given age.

How can somebody that actually research the microcircuitry of the cortex say something that is so blatantly false as this statement is quite an interesting question. It is probably a case of "theory-driven blindness" (Where a theory that a person holds makes him blind to some facts), but if so it is quite an extreme case.

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Yehouda Harpaz
yh@maldoo.com
16Aug2001
http://human-brain.org