Emails - cleaned up formatting + small edits

Peter Kotanen peter.kotanen@utoronto.ca

As Mark Davis indicates, the proposed ms seems to contain some pretty different views. I'd like a clearer idea of how they are going to be resolved. In particular, I'm reluctant to throw the baby out with the bathwater - though I do feel exotics aren't so different as a rule, I don't want to find myself arguing that there are never important differences, or that

I likely could contribute best to discussions of herbivory and possibly native-range processes, including range extensions. However, I am concerned that the subject area is just too big - I think we will need to significantly focus it. I also feel we will need to improve novelty; many of these issues have been discussed for a long time, as Mark Davis suggests.

I'm also concerned that we strike the right balance. I agree that exotics often (usually) behave much like natives. However, this isn't necessarily the case; rather than a "yes" or "no" answer to the issue of whether exotics are different, I think it's better to ask when they are different, and how much any difference matters relative to ecological similarities.

As well, I agree with Dov and others that exotics may have important impacts even if they aren't different. A species that is abundant and important in its native range may have impacts in its exotic range for exactly the same reasons it's important in native areas; nonetheless, these impacts may be serious problems. Ragweed is a good example: it represents a major health and agricultural problem in invaded areas for exactly the same reasons it has these effects in its native region.

These effects don't depend on its status as an exotic, but they are novel in the sense that they are a new problem for invaded areas. I don't want to be interpreted as arguing that exotics don't require a management response just because their effects aren't unique.

I like Marc Cadotte's suggestion that the one way exotics are different is their history; this also seems like it may be an entry point for some new perspectives (e.g., community phylogenetics). I also think it's worth discussing timescale, both for adaptation and for the invasion process itself: one way that invasions differ from natural range extensions is that they are often much faster. Invaders may cross a continent in decades, rather than the millenia typical for post-glacial migrations, for example; what are the implications of this?

One final issue for me is whether we should be studying average behaviour or extremes. Most exotics are innocuous; what practically matters is the exceptions. So is a question as broad as "do exotics differ from natives?" purely of intellectual interest, and should we instead focus on the small subset that evidently do? This clearly represents a selection bias, but nonetheless it often seems reasonable to focus on the worst offenders, as long as we acknowledge that they are the exceptions.

Marc Cadotte cadotte@nceas.ucsb.edu

I think perhaps it starts a little strong -to say the differences are trivial and that we need to search for those that are different. I think that there are important, systematic differences, and to address Mark's 'species are species' view, species carry with them the histories that shape them (this is why comparative analysis must incorporate phylogenetic information -species are not independent of their history). Environmental tolerances, pathogen susceptibilities, anti-herbivore strategies, etc., are constantly evolving but largely predicated on past success. Thus, species 'native' to a region share much of their recent evolutionary history and have faced the past together. 'Exotics' have had other historical trajectories and biogeographic affinities that make them different than the species inhabiting a distant place. For example, the current eastern North American flora has evolved recently under colder (post-glacial) regimes and current invaders may have evolved in places that have been more like today's climate in eastern NA, where they can take advantage of longer growing seasons, etc. Conversely, Egypt's exotic flora constitutes a much smaller proportion of its total flora, despite being open to trade for a much longer period of time, why? You can see how this is germane to climate change, but the logic also works for disease, herbivory, etc., though the evolutionary time frames may be different.

Thus, I think that simple history potentially makes them different, and this allows us to ask why are species from region A having such large success in invading region B. Then history itself is a potential explanation coupled with on-the-ground or trait differences, EICA, novel weapons, etc. Thus a good starting place may be history, and the fact that we know that the origin of invaders in any place are biogeograhically nonrandom. Why are they not just a random subset of the global flora (obvious invasion vectors are an important part of this)?

Given this biogeographic nonrandomness, what history are they carrying with them?

That said, I do agree with the view that these differences are often not qualitatively different and that we may slip into unhelpful thinking, assuming systematic differences (your sec. 3 -pitfalls). Further, exotics are subject to the same broad suites of ecological and evolutionary processes as native residents.

Therefore, I think that clarifying the issues around the ways in which exotics are different, and not different, than natives is a potentially useful and worthwhile activity. It may help clarify thinking on the topic.

One note about potential journal. The Journal of Applied Ecology would require some explicit management consideration, and I'm not sure if this paper would necessarily want to do that. Just something to be cognizant of.

John Parker parkerj@si.edu

I agree with Petr that focusing on the central question of whether exotics are somehow 'different' is where we can best distinguish this manuscript from the numerous other reviews of particular theories of invasion success. 

I just received Mark's email, which I think also raises some important points about how best (or not) to approach ANOTHER invasions review....on a quick read I feel that Mark's email strengthens the point that invasion biologists are generally not focusing on the proper control group: abundant natives. The rest of my email was written before Mark's came through, but I *think* there is still room to make two important points, with Mark's explicitly addressed in the 2nd point below. 

 How do we define exactly what must exotics be different from to show they are 'different'? This seems like a 2 part answer. First, there are lots of studies showing that Invader X alters various ecological patterns in areas with and without X.  As Rob and Cini point out, these may just be species differences, not necessarily differences arising by virtue of a species being 'exotic', which to me has always implied some difference arising because of a non-shared evolutionary history.  Testing whether or not Invader X (alone) is acting differently requires biogeographic work to determine whether X is doing something different away versus at home. It then becomes important in these tests to rule out founder effects versus true "home-vs-away" effects.  As Dov also points out, even if they are not doing something different from an ecological/evolutionary standpoint, they may still be undesirable from a management perspective, ie, species-specific impacts that render the ecosystem different than the way we want it.

Secondly, when taking a multi-species approach to inferring 'differentness', lots of studies have utilized the 'controlled phylogenetic history' approach by comparing congeners of natives versus exotics.  However, I would argue here that these types of studies can be improved by comparing equally abundant native and exotic species from the same environments, many of which will be non-related (as also mentioned by Rob and Cini).  These types of studies can be corrected for phylogeny later using community phylogenetics, plus, in my mind they allow for a better test of whether native and exotic species are being differentially driven by different processes. If similar processes are driving exotics and natives with similar traits, I would argue that exotics are not fundamentally different from natives, but rather that the underlying processes driving ecosystem structure/function are now different (as Mark points out).

At some level this argues for putting invasion biology back into a community and evolutionary ecology framework rather than on its own pedestal, which almost inherently argues for invaders doing something 'different', rather than explicitly testing for differentness.  This point has been made repeatedly in numerous books and reviews, so it would be important to phrase this in a way that is non-repetitive (and positive). 

 Anyways, that's my 2c, which in summary would be to streamline the effort on the 'differentness' question.  I'm keen to contribute and can complete whatever sections are assigned to me, but also open to discussing whether or not such an effort is duplicative or useful. 

Petr Pysek petr.pysek@ibot.cas.cz

To me these contrasting views seem to be a challenge of the whole initiative; I think Cini and Rob outlined a strong central topic and we need to search for EVIDENCE by carefully reviewing literature rather than just writing how we think it works or doesn’t work. We may find out that there are studies that show or do not show difference or that there is little evidence in literature to answer this question (because of inappropriate design, poor data, whatever); even then, to outline a kind of research needed to do so might be a valuable output. That the „authors dichotomy“ in this potential paper starts with some of us considering the very „central question“ valid and others not need not be major constraint, in my view.

Concerning Marc’s note on the venue, would it be better to write the paper first (if we ever get to that stage and then decide?

Mark Davis davis@macalester.edu

As many of you know, I am not keen on another paper focusing on species traits of non-native species.  I really don't see that any outcome will provide much of value to society or that it will do much to strengthen the field.  This partly seems like an effort to keep an old approach on life support.  We really need to move beyond this simple dichotomy of native vs non-native.  With all species experiencing the many types of global change (climate, eutrophication, land use change, all species are, to paraphrase Reise et al. (2006), strangers in a strange land.  Species are species.  Some new ones will be similar, some will be different, some will be different in some ways, others will be different in other ways.  We would be doing a much better service to society if we could begin to focus on species that are causing problems.  Many of these are non-native species; many are native species.  Are there any distinctive and consistent traits associated with these problem species?  I think this would provide more of a service to society.  Other than providing another citation for everyone, I just don't see the value of yet another paper on species traits of native and non-native species. 

All of that said, the outline clearly indicates an interest by some of critiquing efforts made to date along this line.  My reading of the outline suggests that there are a couple of different interest groups, one that is not really very supportive of focusing on differences between native and non-native species, and of the nativism paradigm in general, and one that is still interested in organizing research around the 1983 SCOPE initiatives.  I caution people against trying to write a paper that accommodates all views.  These usually end up being mushy and vague and of little use to anyone, and hence a poor use of the authors' time.  If people have strong views one way or the other, I think they would be better off writing their own strong and focused paper. They can make their case and then the readers can decide whether they were persuasive or not. 

I was interested in the references in the outline that raised the issue of perception and perspective.  As I told David in an email on another matter a couple of days ago, I just read a very interesting book by two very established ecologists: Bill Reiners and Jeff Lockwood: Philosophical Foundations for the Practices of Ecology (Cambridge 2010), which delivers a pretty severe critique of ecology, focusing on issue of perception, perspectives, language, and concepts.  The philosophical treatment gets pretty heavy at times, but its messages and warnings are important to all ecologists.

Sorry for the lack of holiday cheer, but I felt it important to provide some challenge to the initiative.  It's real easy to hop on board a multi-authored initiative such as this, but do people really feel strongly that this manuscript would be able to offer something new and valuable to the field and to society?

Petr Pysek petr.pysek@ibot.cas.cz

Thanks for the outline, I am keen to be involved. I think we need really focus on the central question, i.e. are they different, and look what "objective evidence" is out there in the literature to answer it. I agree with Dov's and Dave's comment and think that we need to define clearly what we mean by "being different". In agreement with Dov's suggestion, to me it is "doing different things than natives where they co-habit" and "doing different things in their introduced range than in the native range".

Dave Richardson rich@sun.ac.za

I did not receive the 20 Dec mail with the outline, but I'd be keen to be involved. I agree with Dov's statement that even if exotics were very similar to natives, the fact that they need to be incorporated into, e.g., seed dispersal, pollination networks (and other webs), means that they will have some "effect"... some may be subtle (at least in the short term)... if they are able to form large populations as aliens their effects will be amplified - I think we should re-visit the Parker et al (1999) equation for impact which posits that I is the product of range, abundance & per capita impact.  Anyway, I am keen to see the outline & to be involved.

Dov Sax dov.sax@gmail.com

Nice job on the outline.  I'd like to be involved and I'm happy to write a section (you can assign one to me). I have a couple thoughts on the ms.  First, I think its important to emphasize that even if exotics were "identical" to natives that they would still cause many changes in ecosystems that we might be unhappy with - particularly if we view natives as existing along a spectrum from dominant to passive players in ecosystems of any given place; consequently, there are really two tasks needed: 1) to better characterize variation in natives (this is an ongoing and traditional topic in ecology and evolution, but perhaps we can identify axes of variation that haven't been specifically addressed often, but that could be done more frequently), and 2) to better characterize how natives and exotics may differ.  Second, I think an important axis of comparison is how natives and exotics differ in a place or region where they co-habitate; this is slightly different than many of the comparisons you make in the outline, but similar to others; I suppose my point here is that we can be clear in identifying different types of comparisons (i.e., A, between exotics in their native and naturalized range, and B, between natives and exotics that cohabitate).