The Appendix Theory of Neurogenesis

We’ve all had “theories”, haven’t we. That’s “theory”, not theory. You know what I mean by “theories”: those not-necessarily-at-all-well-formulated, probably untestable crap ideas that pass briefly through your mind when staring out the window of a bus, or repeat in your mind when you’re trying to sleep. Thankfully for the world, they usually end up going nowhere.

A “theory” of mine that I once considered for an appropriate time of about 2 seconds is The Appendix Theory of (Adult Hippocamal) Neurogenesis. If you don’t know, in the 90s an idea was confirmed, that — contrary to Cajal’s (somewhat disappointing) assumption that brain cells are never born but just die — new brain cells are born, and one of the places that happens is the dentate gyrus of the hippocampus, a structure neuroscientists automatically and immutably pair-associate with memory function. Once AHN was discovered, the critical question for those of us interested in function was what, specifically did these new neurons do for us? What is AHN for?

You’ve already guessed the idea behind Appendix Theory. It is that AHN is vestigial; the young neurons thus formed add nothing to our cognitive abilities. Indeed, these neurons are weird; they are over-responsive and highly plastic and may contribute little to the DG circuitry, other than maybe some noise.

Appendix Theory was immediately challenged and apparently proved predictably daft by experiments that found that knocking down AHN by irradiation or other methods led to impairments in spatial memory. But not everyone got this result: in some experiments knock-down had no effect, a finding consistent with Appendix Theory. A possible resolution to this ambiguity came when it was reported that AHN knock-down impaired the discrimination of similar locations – thought to require the formation of non-overlapping representations through a computational process called ‘pattern separation’ – without affecting other aspects of spatial cognition (Clelland et al., 2009). The previous inconsistencies could now be explained, because the load on pattern separation in these tasks was never controlled – in some studies it might have been high, and in some low (e.g., ambiguous cues in one water maze room, but not another). Appendix Theory received a number of subsequent coffin-nails from other groups reporting that AHN knock-down impairs the discrimination of similar locations/contexts, and indeed that increasing AHN can enhance this function. Support for this function of AHN has now come from several species, using a variety of behavioural paradigms, and from methods including lesions, patient populations, and neuroimaging. Appendix Theory seems to be dead, and right or wrong, a function for AHN in pattern separation has become the assumption.

A new paper, however, could yet breathe new life into Appendix Theory. Groves et al (2013) used a novel method to knock down AHN, and found no impairments on any spatial tasks. How could all of those studies from using all those species, paradigms and methodologies be wrong? It’s possible. For example, methods of knocking down AHN, like any lesion method, could have off-target effects. In Clelland et al, really what we should have done is include a group with selective lesions of the mature neurons in the DG — but I have no idea how that could be done! (Clever suggestions below the line please.)

The trouble is, most of the tests in this new paper – standard spatial tests like water maze and fear conditioning – are irrelevant because, as described above, plenty of people have shown little effect of AHN knock-down, and these past inconsistent results appear to have been resolved by reassessment of those old data in terms of pattern separation. However Groves et al did include a test of pattern separation that had been used previously, a radial maze task similar to that used in Clelland et al.. Unfortunately, for some reason the small separation condition wasn’t more difficult than the large. In another test, the condition that was meant to tax pattern separation elicited significantly fewer errors from the rats. So, it is hard to be convinced the rats in this study were really challenged appropriately. It’s worth noting that in some of the anti-Appendix experiments (including our own), the two conditions were equidifficult for controls. The difference is that those studies found impairments. When claiming no effect, however, it has to be clear the animals were adequately challenged.

Indeed, when claiming a negative a minimum requirement is to show that the behavioural tests used are sensitive to comparable manipulations. The authors argue their tests are sensitive because full hippocampal lesions have an effect. (But in mice, not rats.) I couldn’t find their pattern separation test in any of their other papers, but let’s assume it’s sensitive to hippocampus lesions. Trouble is, a hippocampus lesion is hardly comparable to a lesion of 10% of the cells in the dentate gyrus. Before deciding that all those studies described above are wrong, and embracing Appendix Theory, we need to see that their task is sensitive enough to pick up effects of a comparably sized lesion, ideally in the same species.

One can also reasonably ask whether this new knock-down method was functionally effective at all; after all, the point of the paper is that no impairments were found. There are indeed some effects on elevated plus maze but, as the authors very honestly pointed out, it wasn’t significant at an appropriate level of statistical rigour. To be honest though, that would be a bit of a picky criticism, for at least two reasons. First, if Appendix Theory is correct, there is no prospect of a ‘positive functional control’ because according to Appendix Theory AHN doesn’t have any function! And second, the knock-down of neurogenesis was 98%, which is huge! It seems to me this is the real strength of the study, a new method for creating a very substantial knock-down of AHN.

I should also mention that the authors add to their study a meta-analysis of studies of neurogenesis knock-down. That could be really useful. Trouble is, as far as I can tell the analysis included what appears to be only a random two papers testing pattern separation – and both of these were contextual fear conditioning, which is widely regarded as the most problematic paradigm (no manipulation of the load on pattern separation). Furthermore they failed to consider any study testing the effects of enhancement of neurogenesis, which provides particularly strong evidence for functional efficacy, especially in studies in which the increase in neurogenesis was apparently very selective. In any case such an analysis does not capture the persuasive power of the replication of the finding using very dissimilar methodologies and species, as is the case of AHN and pattern separation.

To conclude, this impressive new method for a achieving a very substantial knock-down of neurogenesis could prove very valuable for studies of the functional role of AHN, and the molecular events associated with it. (Although it should be noted that this method itself had known off-target effects, namely it affects not just neurons, but glia.) For now, though, it is clearly not quite time to embrace Appendix Theory.


7 thoughts on “The Appendix Theory of Neurogenesis

  1. Thanks for this Tim. I did formulate as well my own appendix theory a few years ago. I still believe that the more we go down in the evolutionary scale and more these phenomena of neuronal plasticity appears in the brain. It may be very well the case that the appendix theory is wrong for rodents… But what about humans? This is the real challenge and in particular when we think about new treatments for CNS disorders. Cheers! Max

  2. Hi Tim,

    I haven’t read the Groves paper, but my personal theory (theory in the sense described here) borrows from many others. Mainly that neurogenesis helps in avoiding catastrophic interference and in flushing out old memories. A commentary by Paul Frankland in response to Urbach et al. (2013) points out that behavioral tests must fall with in newly generated neurons’ critical period where they are functionally mature and are being recruited to memory traces.

    However, no deficits may be seen even if experimenters do perform tests in this period. My response to this is that for a lab rodent, largely deprived of experience who need learn only a very limited amount of information (e.g. This arm for reward or that arm) in comparison to wild animals may not need the plasticity afforded by neurogenesis to do so, effectively operating under the cognitive budget. In these circumstances, the limited plasticity of older dentate granule cells, or perhaps more importantly, of neurons born just before the manipulation, may sufficient to sculpt hippocampal representations. Might a relatively large learning load drawn out over time be significantly impaired after ablation?

    Further, there are two separate questions surrounding neurogenesis: 1) what do highly excitable, highly plastic neurons bring to the DG circuit and how does this differ from the function of older granule cells and 2) what impact does new neuron addition and (less established) subtraction have one established hippocampal memory traces? From my understanding, experimental studies have largely focused question 1 and computational models question 2.

    I also wonder, if the Appendix Theory described here were indeed true, and neurogenesis has no ROLE in cognition, might it anyway have an EFFECT on hippocampal processing?

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