In praise of a novel risky prediction – Biosphere 2

You have probably heard of Biosphere 2  (so named because you are living and breathing in Biosphere 1). It is based north of Tucson, Arizona. It is an entirely gas-impermeable living environment covering 1.27 hectares with rain forest, coral reef, desert, savannah and farm ecosystems designed to support 7 or so humans in perpetuity with no external inputs except energy. The facility is a marvel of engineering (as it probably should be for its $200 million price tag).

A picture of part of Biosphere 2

A picture of part of Biosphere 2. The dome on the left is one of the two “lungs” (a giant air bubble under a 20-ton rubber membrane to allow the air to expand and contract without blowing out the glass).  The desert biome is under the glass on the left (set back), the marsh and ocean biomes are under the longer glass section to the fore and right in this image (with the savannah running across the backside). The rain forest is off the image to the right and the farming biome (now the LEO experiment) and living quarters are out of view behind. (image by user Gleam on Wikimedia under CC3 license)

What most people know about Biosphere 2 is how it was covered in the news when the first crew of 8 people were sealed in for two years from 1991-1993. (there was a follow-on mission for 6 months that received much less attention). Press coverage was initially favorable. But over time, squabbles within management and within the crew, two injections of oxygen that were not revealed in a transparent way and even rumors of the crew ordering pizza and opening the door to receive it during their mission took their toll, and the project was mostly treated as a joke in the press. This decaying reputation led to the need to hand the facility over to Columbia University who invested but then left (which didn’t help the reputation).

Currently, Biosphere 2 is owned and operated by the University of Arizona. Full disclosure: as somebody who was on the faculty at UA I have colleagues who include a former director and one of the current faculty at Biosphere 2 and several other faculty running experiments there now, but these ties are all related to the very recent UA management of B2 and have nothing to do with the period I am writing about (except for the paragraph on LEO below). I have visited it twice as  “tourist” but also several times on scientific tours. I last visited it as a tourist during my vacation a couple of weeks ago which got me thinking about what a great contribution to ecology Biosphere 2 has made (in contradiction to its reputation).

I have argued in the past for the need for prediction in ecology (see these posts: IIIIIIIV). I have also made no secret that philosophically, I am a fan of Lakatos. Lakatos was a student of Karl Popper who rejected Popper’s notion that the main goal of science was to falsify theories. Lakatos argued that science progress when theories make predictions and these predictions are tested and confirmed. And Lakatos was quite clear that there was a spectrum from weak, boring predictions that wouldn’t sway anybody (fertilizer will increase yield) to “stunning” predictions (Newton’s predictions that Halley’s comet will return in 76 years or there will be a planet located near where Neptune was found).

In this framework, I think Biosphere 2 has to be labelled a resounding success in sticking out its collective neck and making truly “stunning” predictions*. Although these predictions in many ways did not prove true, we have (and this is the point – see especially this post of mine on prediction) learned an enormous amount from the failed predictions.

On the applied question of can we build a human-supporting self-sustained ecosystem, the answer is no, not yet. But we learned a lot. Biosphere 2 taught us that concrete takes years to fully cure (which is what was pulling the oxygen out  – but something engineers did not really understand since they hadn’t built concrete in enclosed environments at any large scale before). Organic farming knowledge is essential (the first mission had nobody trained in organic farming and had many crop failures and resulting hunger – something corrected on the second mission). Attention needs to be paid to the social dynamics of small, enclosed crews.

But it is mostly the ecological failures=learnings that fascinate me.The glass blocked ultra-violet light which led to most of the pollinators congregating near the glass boundaries and dying (and the humans having to do a lot of hand pollination). The rain forest, unlike real rain forests, accumulated enormous amounts of leaf litter due to missing microbes (and then things jump started and normal high levels of litter decay are now occuring (we still haven’t figured out exactly why). The coral reef crashed and burned for reasons that are still being worked out. The trees were not exposed to wind with interesting implications for growth forms and wood density. An invasive species of ant that snuck in through the soil obliterated much of the intended insect community. And etc. An entire special volume of new research was produced in the early days, and research is ongoing. The number of questions one could and should address is limited only by funding.

One cool success where the applied and basic intersected was addressing the oxygen deficit. The oxygen deficit was seasonal and worst when the biomes were shut down for winter. The crew was able to manipulate the arid (desert and savannah biomes) by adding water at the right time to green up out of season with the rainforest (thereby releasing some oxygen) to help ameliorate the oxygen problems.

And to the University of Arizona’s credit, they are continuing in the tradition of bold, risky predictions. In the former farm biome they have built LEO (Landscape Evolution Observatory). They are building three hillslopes (each with 333 m2 of surface area and about 1,000 metric tons of soil that are massively instrumented). They are starting with virgin soil and gradually introducing biotic factors to test theories of water flow, erosion and etc. Traditionally hydrologists have had to deal either with very small trays or the real world which is not fully controlled and instrumented. This meso-scale, controlled-environment experiment has already blown holes in current models and understanding of erosion and underground water flow and they’ve only simulated one rain event!

So far, I have talked as if the applied goals (self-sustaining environment for humans) and the basic research lessons were distinct. But I actually think they are highly complementary. I think this is exactly where ecology needs to head as we become more predictive. Specifically, ecology needs to stick its neck out making risky predictions and one way to push ourselves is to be involved in eco-engineering projects (whether they be restoration or self-sustained enclosures or reserve designs or green infrastructure like green roofs, etc). I think this for two reasons.

  1. I think this will help the public reconnect to and appreciate ecology again. This can’t hurt our funding. But even more importantly, it can’t hurt the role of ecology in policy and the public imagination. Such places where humans and ecology interact capture the attention of and inspire the general public. Biosphere 2 has been criticized as performance art (and indeed a large number of the original participants had theater backgrounds). But maybe we need to be more aware of the performance art aspect of our science. Physicists build giant “atom smashers” and talk about “god particles”. Astronomers talk about asteroids smashing into the earth. Pulling off the moon landings gave engineers a degree of increased credibility that has lasted for generations. Where’s the exciting places ecology interacts with humans? I think eco-engineering a self-contained, human-supporting ecosystem that could be used to go to the stars is one place!
  2. Aside from capturing the imagination, I think eco-engineering is good for the science, even basic science. Specifically it forces us to stick our necks out and make Lakatos’ stunning predictions. Very often, these result in stunning failures. But these failures advance science just as much as the successes. Sometimes more. Again, as noted in this post, the pressure to make daily weather forecasts and bear the burden of publicly being wrong has been very good for the science of meteorology. I think it would be good for the field of ecology too.

What do you think. Should ecologists be involved in eco-engineering? Is prediction good for science? Are failed predictions good for science? What bold eco-engineering project to fire the public imagination should ecologists take on next?

*Which is not to say there weren’t a number of avoidable disasters too. There could be a whole post in itself analyzing the strengths and weaknesses of launching a project managed by two strong-willed, visionary people who had conflicting goals from the start and funded by a billionaire with all having an eye to publicity vs the much more staid, science-focused, half dozen rounds of peer review of something NSF would try to pull off.

45 thoughts on “In praise of a novel risky prediction – Biosphere 2

  1. Hi Brian,

    Interesting to hear about this. I recall reading about the original project and Columbia’s takeover, and being skeptical that we were likely to learn much from an unreplicated experiment with no controls.

    My feelings are more mixed now. I appreciate the argument that eco-engineering is maybe the best test of our understanding of ecology. If you really, really know how ecosystems work, you ought to be able to build them to spec, diagnose and repair them when they break down, and identify and predict the failures of unworkable designs. And you’re right to point out that, in general, engineers manage to diagnose and learn from the failures of their designs without doing lots of replicated experiments. But I wonder if ecological systems are the sort of systems one can learn about in that way. Or maybe they could be, but we don’t know enough yet to learn about them in that way.

    Re: the performance art aspect of this and how it could attract public attention, intriguing suggestion. But as you note, the attention paid to Biosphere II quickly turned to mockery, and then faded away.

    A thought, following on from the previous two paragraphs: maybe the right comparison here isn’t physics and engineering successes like the moon landing or the Large Hadron Collider. Maybe the right comparison here is something more like the many failed attempts at heavier-than-air flight (at least some of which were mocked at the time, if I recall correctly).

    • Hi Jeremy – interesting that you should say you’re “skeptical that we were likely to learn much from an unreplicated experiment with no controls” and later mention the LHC, which is effectively an unreplicated experiment with no controls! In fact the published evidence for the existence of the Higgs Boson rests on a single run of the LHC, as far as I can gather.

      This has been much on my mind of late: we recently had a manuscript rejected from a high profile journal, without going to review, because the editor was unhappy that we used one control and one experimental site. It was a large scale study of removal of floral resources (in fact I think I’ve mentioned it to you before) and the first of its kind to assess the stability of plant-pollinator networks in this way.

      My argument to the editor was that, as with the LHC, low-replication experiments such as this have value if they then stimulate further research to test the predictions from it. He wasn’t convinced.

      • Hi Jeff,

        I’m not a particle physicist, but my understanding of the LHC is that it’s not correct to think of it as a single unreplicated experiment with no controls. Rather, the way to think about it is as a single instrument in which many, many experiments have been run. That’s a very rough summary, obviously, but I’m sure there must be some less-rough-but-still-accessible scientific and statistical summaries somewhere in the physics blogosphere.

      • I have to agree. Replication is nice. But it is not a must have to science (at least over the grain-size of a single experiment). Especially in the real world where there are trade-offs such as plot size vs replication. Sometimes replication must be traded for scale.

      • Thanks Brian. What made it particularly irksome was that I pointed out to the editor that the journal had recently published a study based on a single, unreplicated hummingbird-plant network. According to the editor this was ok as it was an observational study rather than an experiment. I gave up at that point.

  2. Hi Brian. Have you read the recent science fiction novel 2312? In it, humans have terraformed asteroids into life-supporting biomes, with different worlds representing reproductions or mixes of Earth’s major biomes. Interestingly, the author presents these worlds as a type of performance art. In fact, in his future world, the word “abramovic” – taken from the artist Marina Abramovic, I assume – is a verb regularly used in conversation. Although I have’t read a lot of science fiction, my own sense is that creating new worlds (e.g. moon or mars colonies) is such a part of public consciousness that we’re inevitably headed there. At some point, ecologists are going to be part of that vision.

    • “At some point, ecologists are going to be part of that vision.”

      The question is whether that point comes before or after engineers repeatedly try to approach it as an engineering problem and repeatedly fail! I’m thinking for instance of recent talks at the Ecological Society of America meeting by Jon Shurin and Val Smith. They talked about how all the engineers working on algal biofuels are struggling to implement expensive engineering solutions to what are really ecological problems. For instance, you want to keep zooplankton from running amok in your bioreactors and eating all your algae? Don’t try to somehow engineer a system that prevents zooplankton from ever colonizing–just add minnows to eat the zooplankton! (Val Smith has done this and it works great, apparently).

      I can think of lots of similar cases. Thinking for instance of molecular biologists approaching various problems from an engineering-type perspective and failing because they didn’t think about the evolutionary aspects of the problem. Same thing often happens with medical doctors, particularly when it comes to managing evolution of drug resistance.

      Not that ecologists and evolutionary biologists are infallible, obviously–but as you say they do have relevant expertise that we’re going to need to draw on at some point. Sadly, the above examples suggest that that point will be later rather than sooner.

      Out of curiosity, anyone know how involved ecologists were in the design of Biosphere II?

      • I think it is fair to say that scientists generally and ecologists in particular were neither at the center of things nor involved early. My general feel is that they were sort of brought in ad hoc at the end.

  3. A few further thoughts, in a separate comment since they didn’t really fit with the thoughts above:

    Back in grad school, I remember Peter Morin saying that they ought to just treat Biosphere II as a massive controlled environment chamber and run replicated experiments inside it. Experiments too big to run in ordinary controlled environment facilities. Sounds like that’s basically what’s happening now, with the hillslope work. Which is quite different than the original intent, and much less bold in some sense, isn’t it?

    Re: the importance of sticking our necks out and making predictions, I confess I’m unclear what the prediction was for Biosphere II. Simply that it would work as intended, without any massive failures like plummeting oxygen or lack of decomposition or lots of species dying out?

    Re: boldness of predictions, it seems like there are different senses of “boldness” here that are being conflated–perhaps intentionally? I confess that I tend to care less about boldness (in any sense) than about severity and learning from error (Deborah Mayo’s work). Can we diagnose why our predictions failed, and so learn something from our errors? Do our predictions comprise severe tests of our hypotheses, meaning that only true hypotheses would pass the tests? Etc. I ask about this in part because it’s always seemed to me that Mayo’s philosophy of science is much like engineering in spirit (I don’t know if she’d describe it that way herself, but that’s how it feels to me). And so it seems like a more natural fit to eco-engineering efforts like Biosphere II. In contrast, at least some ways of being “bold” would seem to inhibit rather than promote learning from error. If you try to do something that nobody’s ever done before, relying on a lot of guesswork because the relevant theory and background knowledge just isn’t there, that’s a very “bold” thing to do in the sense that you’ll probably fail. But precisely because the relevant theory and background knowledge isn’t there, you may well not be able to learn much from the attempt besides the brute fact that it failed. So I wonder if you could talk a little more about how you see “boldness” of predictions relating to “informativeness” of failed predictions.

    • In general I would expect a microcosm person to have some sympathies towards eco-engineering and Biosphere 2. It shares the constructed, controlled context as a way of doing science. It seems like you see this as well, although you identify differences in replication.

      It is interesting to compare Mayo’s “severe” with Lakatos’ “bold” or “stunning”. I think they have more in common than not. Both emphasize really putting a theory to a strong test. Weak predictions not accepted in either approach. The biggest difference I see is, at least as you describe severe, it focuses on direct traceability to one hypothesis. Whereas Lakatos with his research program paradigm was definitely moving away from single hypothesis testing. To him a bold prediction is more or less the same as risky. Something where we don’t already know the answer. Something that will really make you impressed with the theory that made the prediction if it comes out true.

      • “Something where we don’t already know the answer. Something that will really make you impressed with the theory that made the prediction if it comes out true.”

        Hmm, to my ears this sounds rather unlike severity. For one thing, it suggests some notion of prior probability of hypotheses, which of course doesn’t enter into Mayo’s framework. It also suggests that it’s properties of the hypothesis or predictions that determine whether we’re impressed if they’re true. In contrast, I’d say that whether we’re impressed depends, or should depend, on the properties of our *tests* of our hypotheses. I’m thinking for instance of the Higgs boson and other successes of particle physics. One could argue, I think, that the prediction of the Higgs was not bold at all. Standard theory, which had been already passed many severe tests, predicted it. So while we didn’t already “know” the answer, we certainly had very good reason to expect to find the Higgs–the shock would’ve been *not* finding it. But I find the discovery of the Higgs tremendously impressive, because it was a really severe test of the theoretical prediction. A test that only a correct theory could’ve passed.

        I dunno, I still have trouble getting what it means for a theory or hypothesis to be “bold” in a sense that matters for scientific inference, and that’s distinct from “allowing a severe test”. It’s one of these ideas that initially seems quite intuitively appealing, but then as I think more about it and try to elaborate it and pin it down it sort of slips through my fingers. “Fruitfulness” of theories is the same way for me.

      • I have to agree with Benjamin re the Standard Theory predicting the existence of particle never before observed or speculated about as bold.

        In general I think I’m being unclear/you’re misinterpreting novelty of predictions. Take the following:
        1) If I add this chemical to this plot, something will happen
        2) If I add this chemical, biomass will increase
        3) If I add this chemical, biomass will increase 4.2-fold
        4) If I add this chemical, the herbs will increase faster than the trees, shade out all seedlings and take over the plot in 50 years.
        Which of these is a more severe test? Which of these is a more bold prediction (Lakatos also talks about “risky”- so which is a more risky prediction). I think the answer to all three questions would be #3 & #4>#1 & #2, no?

        Wouldn’t you describe Newton’s prediction that there must be a planet of approximately a certain mass at a certain location in space which was then confirmed with the discovery of Neptune as both a severe and a bold/risky prediction?

      • Jeremy, if you haven’t already you should check out “Against Method” by Paul Feyerabend. I suppose would’ve suggested the Biosphere scientists should be spending their time in the box thinking outside the box…

      • I am not a physicist, but I don’t see how predicting the existence of a particle never before observed, is NOT a bold prediction. The general public has seemed to be quite impressed, and apparently the nobel committee thought it was a pretty big deal too. The fact that we were so confident to find it 50 years later speaks more to the success of the Standard Model.

      • @Dan Linden:

        “Jeremy, if you haven’t already you should check out “Against Method” by Paul Feyerabend.”

        Yes, I suppose I should. It’s famous. I’ve read about it. But the trouble is, some of what I’ve read makes it sound very strange–provocative, but not always in a good way. So it’s on my list, but first I need to get to some of Feyerabend’s precursors. I first want to read some Popper first hand (I hear that he’s different than, and more sophisticated and nuanced than, the n-th hand versions that are popular with scientists). And then probably some Lakatos. If only so I can quit not quite getting what Brian’s on about whenever he brings up Lakatos. 🙂

        @Benjamin Martin

        Oh, I can definitely see why one would want to call the prediction of the Higgs “bold” in some sense! I’m just trying to pin down *precisely* what that sense is. For instance, the prediction of the Higgs wasn’t bold in the sense of “contrary to our current theoretical understanding” or bold in the sense of “you can’t find any experts who think that that prediction will hold up”. So yes, it was bold–but in some other sense. And while I’m sure I sound like a total pedant about this, I do think it’s worth trying to be as precise as we can about this, because different senses of “bold” will have different implications for scientific practice. For instance, I agree with Brian that we should seek to test predictions that are bold in the sense of “quite precise, quantitative, and detailed”, and that we should be impressed with theories that pass such tests. But I think that’s quite different than seeking to test, say, predictions that are “bold” in the sense of “nobody thinks that prediction will hold” or “if that were true, it would contradict everything we thought we knew about that phenomenon”.

      • @Jeremey

        I agree bold may not be the most precise term, but I think the “something that will really make you impressed with the theory that made the prediction if it comes out true” in part encompases “severe”. For example, predicting an outcome that could arise for many reasons is generally less impressive than one that could only emerge from a smaller set of mechanisms. But it also could include predictions that are not “severe”, for example, if some complex, big-data-driven, machine-learned model turned out to be able accurately predict future events (weather, population dynamics, etc.) we would be impressed, but if turned out to not be wrong, we would not be able to identify what went wrong.

  4. Hey Brian,
    Another apt axiom is that the best way to learn how to do something is to have to teach it to a class of 500 undergraduate non-majors. A true test of our understanding is our ability to recreate or fix broken ecosystems. It certainly would make us more useful, and the planet could certainly use more useful ecologists right now. But we have to be willing to fail, sometimes spectacularly in a controlled setting, to learn how things work. That said, there are a number of psychological tides we swim against.

    First, given the legal requirement for reclamation, the fuzziness in what a reclaimed environment will look like, and the profit motive of those in extraction industry, there is a lot of dubious reclamation work being done (see recent article about Margaret Palmer and SESYNCH in Science). Not surprisingly, this has not made the terms “reclaim” or “restore” particularly popular among our colleagues.

    Second, I think a lot of ecologists love the variability and complexity. In fact, many are almost proprietary about it (one bioassay is to ask their opinion about neutral theory). The notion that we have reached that level of understanding that we can reclaim/restore is, for them, ludicrous or more.

    Third, I think you are absolutely right {Mike extends the secret Lakatos salute to Brian} that, to the extent that many ecologists think about hypotheses/predictions, they are morbidly afraid of being wrong. But testing fundamental assumptions and predictions, especially simplifying ones, gives us the best framework to learn something new when those predictions go down and the hypotheses fail. That is the point, isn’t it? All of us can recall a time when a cherished hypothesis failed, leading to the four stages of bereavement–shock, denial, grieving, acceptance–followed by…enlightenment: we actually *learned* something with this experiment, we weren’t just *confirming* our pre-existing bias. Those shocks of discovery are every bit as exciting as the smug satisfaction when, hypothesis supported, “we knew what was going on all along”.

    It would be interesting to have an informal network of ecology departments that each adopt a beat up couple of acres or so, perhaps a city lot. Identify some reclamation criteria. Then generate some bold predictions–the native vegetation is dispersal limited; it is limited by the availability of N; soil compaction… invasive species X…–and set about to test them. Most of the first hypotheses would, in years time, be seen as hopelessly naive. But that, I suppose, is the point.

    • I recall reading a review many years ago (book chapter from Julie Lockwood and Stuart Pimm–1997, maybe?) where they compiled all the data they could find on the success of ecological restoration projects. What were the indices of success, and were they achieved? As I recall, what they found was that restoration was often successful if success was defined as restoring the previous plant biomass or primary productivity. Basically, if you want the land to be green again, and don’t much care what makes it green, we’re pretty good at that. Restoring species richness was more rarely attempted, and much harder. Restoring species composition was more rarely attempted still, and basically never successful. Not surprising, perhaps, and I’d be interested if anyone’s done a similar review more recently (anyone know?) I’d be curious if we’ve gotten better over time at hitting more difficult restoration targets.

    • I agree that restoration projects in the abstract as I’m talking about in the post and restoration projects in the real world as funded by coal mining companies etc are different enough they maybe shouldn’t e called the same name. But as Jeremy’s comments add – restoration in the pure sense is not yet something we’re good at – it is a real challenge to current ecological knowledge.

      You are too right about ecologists reveling in the complexity – “it’s so complex we’ll never understand it!” said with great glee and pride. While I like ecology because its challenging, I certainly hope to have a sense that our understanding (and yes our ability to do practical things in the real world) has advanced over my career. Complexity should not be a cop out.

      Its funny I (like probably many parents) tell my kids that “I learn more from my mistakes than my successes” and I believe it when I say it. But we don’t apply that in science very often!

      I love the mass-ecologist movement to adopt plots of ground and do something societally useful and scientifically challenging with them!

  5. Nice post Brian – I’d read a lot about Biosphere II in the early days then finally got to visit it during an ESA meeting in Arizona over a decade ago, and was impressed by the scale and ambition of the project. Good to hear that it’s still being used.

  6. Re: replicated experiments and engineering closed, self-sustaining ecosystems, a microcosmy colleague once put in a grant proposal to NASA to basically just set up a bunch of microcosms, seal them airtight, and then keep them in an incubator to see how long they lasted. It didn’t get funded as far as I know. Which is kind of a shame, really, since I think this could actually be a useful and informative experiment. And I also bet that you’d get a lot of variation in how long putatively-identical microcosms lasted (think of Jim Drake’s work showing huge variation in how long small replicate Daphnia populations persist even in constant environments in the lab). Which in itself would be a useful result, as it would illustrate the limits of thinking of “eco-engineering” as a purely engineering problem.

    • At biosphere 2 in one of the visitor exhibts there are actually a number of flasks that were sealed over 40 years ago and still going. I forget the name of the scientist who did this, but it was apparently a pet project of his.

      • Ah, so that’s why the grant was rejected–lack of novelty! 🙂

        I think the proposal was actually for something a bit more sophisticated. Seal up flasks with lots of different numbers and combinations of species, different culture media. Periodically unseal some of them to get time series data on species abundances and other variables. But yeah, I wouldn’t be surprised if lots of people have tried this sort of thing. Heck, you can buy novelty paperweights with microbial ecosystems in them, that last for a couple of years from what I hear.

      • Oh I agree – something much more interesting than what I reported could be done. I’d vote to fund it. (Although the 40 years part I did think was especially impressive).

      • “Although the 40 years part I did think was especially impressive”

        Yes, that is impressive. Even if I were to seal up a massive number of my microcosms, with all sorts of different species compositions and culture conditions, I wouldn’t expect any of them to last close to 40 years. Maybe I should try it and see! 🙂

  7. Really interesting post Brian. I agree that prediction is good for science, as is failed prediction. This may seem a bit far afield from your post, but I see this aversion to prediction and especially failed prediction played out in discussions about the usefulness of Population Viability Analysis (PVA) as an aid to management decision-making. As others have pointed out, many critics of PVA ask the question, are PVA predictions true, when the more appropriate question is, are PVA predictions useful. I say, the answer to the latter is an unequivocal “yes”, especially in the sense that you discuss – making predictions and “sticking ones neck out” by acting on those predictions is a way to move forward using our best (but inevitably flawed) tools and learn from the results. I think applied ecology, in all its guises, would benefit from more discussions about prediction, uncertainty, and risk.

    On another note, I think the discussion in the comments above about Lakatos vs. Popper and severe vs. bold predictions sets up false dichotomies. From my perspective, science will move forward when Popperian AND Lakatos-type experiments are carried out and when experiments with “direct traceability to one hypothesis” AND experiments that may test multiple hypotheses simultaneously when “we don’t already know the answer” are all used to advance our knowledge.

    • PVA is certainly useful, in part because stimulates thinking and scenario analyses are particularly helpful. However, most extinction NOT predictable by the naked eye are at least yrs if not decades away. Validation is thus pretty rare.

      • Simone,
        I agree with you about why, in part, PVA is useful. And I agree that validation is rare and often impossible, but the question is, where does that leave us? And this is where I part ways with many critics of PVA. I do not believe validation is necessary for PVA to not only be useful in a pedantic way (as you point out), but also useful in making management decisions. That’s why I like how Brian talks about prediction and risk – our models don’t have to be 100% “right” or safe (i.e., all aspects immediately verifiable) to be useful in a pragmatic way and to advance science and management. Of course, when we’re talking about applied ecology and management, there are risks involved in making the “wrong” decision, and thus we also need to use risk management strategies (weigh the risks of different management decisions against one another and against the risk of inaction).

      • I agree, i.e. I wrote about scenario analysis, which is a more interesting outcome of PVAs than either the “absolute” prediction itself or the validation of the model. However, I do not use the term PVA anymore, it is pretty 90s, I prefer prediction of extinction risk.

  8. I agree that ecologists should be involved in eco-engineering. This is due to the fact that as a society we are unready to address the “elephant in the room”; pressure of human numbers is the main cause of habitat decline, but cultural or religious taboos often prevent this factor from being included as a topic in international fora. Therefore, we will eventually run out of real-estate. Despite NASA’s ambitious plan to colonize mars projects such as Biosphere 2 address the reality; we can’t even successfully do this on earth. I believe we have much to learn on the applied question of can we build a human-supporting self-sustained ecosystem, and I think once we have tackled this in the terrestrial environment we should move into more hostile environments like undersea habitation and agriculture before we tackle the final frontier (space). We may be running out of habitable space on land, as well as arable land but think of all that potential real-estate on the bottom of the ocean!

    • Re: humans just running out of room, that depends on a lot of background assumptions and value judgements about how humans will live, will want to live, or should live. Joel Cohen’s How Many People Can the Earth Support? is good on this. I agree it’s a huge issue, but it’s one that goes well beyond ecology, or science, I think.

      Agree that success in eco-engineering and restoration here on earth seems like a prereq for pulling it off in space. Perhaps unless all you’re aiming for in space is some non-self-sustaining agricultural systems maintained via external inputs.

  9. Watch as I expertly set Brian up to annoy people by giving him a loaded, unanswerable question:

    So Brian, given the choice, would you rather have NEON, or two more Biosphere II’s? 🙂

  10. In response to Jeff Ollerton’s comment that LHC is unreplicated… that is completely false and Jeremy is correct. No debate to that. All the various atom smashing events are indeed replicated events governed by what one can reasonably call a stochastic process. Hence, replication.

    • Can I just clarify what you’re saying here: the individual events that occur during each run of the LHC are considered to be replications within the experiment? It’s an interesting definition of “replication” that had not occurred to me. The parallel in ecology, it seems to me, would be that each time an aquatic organism in a microcosm eats another organism, that’s an “experiment” therefore we only require one microcosm to run a whole set of experiments. Am I understanding this correctly?

      Just to clarify what I was getting at: by “unreplicated” I meant that as far as I’ve been able to ascertain (and it’s difficult to unpick this from the available sources, so I may be wrong) evidence for the existence of the Higgs Boson was based on the output from a single run of the LHC.

    • @setting the record straight:

      We’ve blocked a recent comment of yours (under a different pseudonym, but from the same IP address), because in our view the tone was out of line and because it included an irrelevant and ungrounded pre-emptive attack on our comment policy. Had you provided an email address, we’d have emailed you to suggest how to modify the comment appropriately, since it included a lot of material we’re happy to publish. If you check out the threads on various posts, you’ll see that we never block comments on the grounds that they disagree with the post.

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