Are there Buddy Holly ideas? (or, has any line of ecological or evolutionary research ever been prematurely abandoned?) (UPDATE)

One of the things this blog is known for is calling for the death of zombie ideas–ideas that should be dead, but aren’t. Here, “death” basically means “no longer basing any research on the idea.”

Here are two common ways (among many others) in which some readers have pushed back against those posts:

  1. You have a point, but you’re throwing the baby out with the bathwater. Yes, idea X is a zombie idea–but idea X is only a part of some broader topic on which we need further research. In calling for researchers to abandon idea X, you risk them abandoning worthwhile research on the broader topic. For instance, this is part of Doug Sheil and David Burslem’s response to my critiques of zombie ideas about the intermediate disturbance hypothesis.
  2. You have a point, but abandoning an entire line of research is too radical a solution. What if you’re wrong about idea X being a zombie? Abandoning an established, ongoing line of research is really risky–what if we’re giving up too soon? Science is hard and it’s normal for a research program to run into obstacles. The only way to make progress is to try as hard as we can to overcome them, not to give up as soon as we encounter them. Brian’s made this argument before.

Both responses highlight the downside risks of abandoning a line of research. And it’s absolutely correct to consider those risks. But of course, just saying “there are downside risks” isn’t enough to determine a course of action, because all courses of action have their own downside risks (and their own upsides). For instance, while we don’t want to throw the baby out with the bathwater, we do want to throw out the bathwater. And while there’s always the risk of giving up on any line of research too soon, there are also risks of giving up too late (e.g., because time, money, and effort spent on a lost cause would be better spent elsewhere).

These are difficult judgement calls to make, and so there will always be disagreement about them.* One way to make these sorts of judgement calls is by drawing on our background knowledge of other similar cases. We’ve talked a lot on this blog about zombie ideas, ideas that should be dead but aren’t. But what about the opposite kind of case? That is:

Has any line of ecological or evolutionary research ever been prematurely abandoned due to criticism from those not pursuing it?

Prematurely abandoned lines of research are the flip side of zombie ideas. They’re dead ideas that should be alive. Ideas that, tragically, left us too soon. I propose calling such ideas Buddy Holly ideas. πŸ™‚ (UPDATE: by “prematurely abandoned”, I mean a line of research that was widely pursued but was abandoned prematurely due to external criticism, analogous to how Buddy Holly became popular but then died in a plane crash. I don’t mean lines of research that were never widely pursued in the first place, even if in retrospect they should’ve been. Such lines of research are more like a singer who never gets discovered.)

Of course, in order to make a strong case that an idea really was prematurely abandoned, it probably needs to be an idea that was later taken up again, successfully. Because unlike Buddy Holly, scientific ideas never perish totally by accident, but always for some reason. So you need to make the case that, even though an idea died for a reason, it wasn’t a good reason.

Note as well that, in order for the subsequent revival of an idea to count as evidence that it’s “death” was premature, the idea needs to be revived in something close to its original form. For instance, while modern research on non-genetic mechanisms of inheritance (maternal effects, DNA methylation, etc.) sometimes is called “Lamarckian”, I think the connections between this modern work and Lamarck’s ideas are far too loose and vague to say that Lamarckianism was prematurely abandoned only to be subsequently revived. Similarly, I think it’s a stretch to call modern evolutionary developmental biology a revival of 19th century German idealist biology (“bauplan” and all that). After all, basically any line of scientific research is going to have some historical antecedent. I mean, there were people who thought that Charles Darwin got his ideas from his grandfather, or from Buffon, or whatever! I’m talking about something much more specific than that.

In an old post I suggested Darwin’s theory of evolution as a possible example of a Buddy Holly idea, since it was “eclipsed” in the late 19th century only to be subsequently revived. Although one can argue about how good an example it is.

Probably the best example of a Buddy Holly idea I can think of is group selection getting abandoned in the late 1960s and ’70s in the wake of criticisms from folks like G. C. Williams and John Maynard Smith, and then revived by folks like David Sloan Wilson. You could interpret the history here as a case of throwing the baby out with the bathwater. Abandoning not only naive, good-of-the-species thinking that really did need to be abandoned, but also viable group selectionist ideas. But I’m not an expert on the history here (which in any case tends to be read differently by different people, I think), so perhaps others can comment.

Perhaps research on food web topology might be an example of a Buddy Holly idea, but I don’t think so. Briefly, back in 1977 Joel Cohen had the creative idea to think of food webs as mathematical objects called graphs (aka networks), with species as “nodes” and predator-prey relationships as “links” connecting predator nodes to prey nodes. Food web data compiled from the literature suggested some surprising general properties of these graphs–for instance, they tended to be “interval”, and the ratio of links to species seemed to be constant (Cohen 1989). And Cohen and others developed simple models to try to explain these apparent patterns. However, the data were of low quality, leading Gary Polis and others to argue powerfully that food web theory was a house built on sand (Polis 1991). But the obvious response to this critique (indeed, the response recommended by Polis himself) was not to abandon this line of research, but to go out and collect better data on who eats whom. Which a lot of people did. Explaining the new patterns in those data subsequently motivated a whole new generation of food web topology models (e.g., Williams and Martinez 2000). So rather than seeing this as a line of research that was prematurely abandoned and then subsequently taken up again, I’d see it as a line of research that only remained productive by taking well-founded criticisms to heart.**

Maybe “randomized null models of species x site matrices as a tool for inferring competition” might be an example of a Buddy Holly idea? Depending on whether you think the revival of interest in that approach since the mid-90s has been productive, or whether you think this approach still is open to some of the same fundamental objections that were raised against it in the late ’70s and early ’80s (I basically take the latter view, but your mileage may vary).

In summary, it looks to me like Buddy Holly ideas are pretty rare, and rarer than zombie ideas. Once a critical mass of researchers decide to pursue an idea, they hardly ever give up on it too soon. Which suggests to me that we don’t really need to worry much that debate and mutual criticism will lead to productive lines of research being abandoned. But what do you think? Are there “Buddy Holly ideas”? Lots of them? Looking forward to your comments.

*If you want to argue that no line of research pursued by professional scientists is ever so unproductive as to merit abandonment, well, ok I guess. But that means you’re ok with not calling for the abandonment of research on ESP, Bigfoot, and tabletop cold fusion, never mind more debatable cases. Or I guess you could say that some lines of research should be abandoned, but that other scientists shouldn’t say so publicly–that it’s best to just publicly ignore lines of research you don’t like. If you can’t say something nice, don’t say anything at all, as the saying goes. Which again, ok I guess. It’s fine if some folks adopt that as their own personal policy. And perhaps in some circumstances it’s the most effective way to encourage abandonment of unproductive lines of research. But personally I’m a little uncomfortable with any argument that says scientists should remain publicly silent about their scientific views, or should never publicly criticize one another’s scientific views. I’m actually not sure if anyone holds such extreme “anti-criticism” views, so I might be addressing a bit of a straw man here. But I’m a believer in thinking through extreme limiting cases, even if they never actually occur in the real world. πŸ™‚

**It probably helped that the criticisms could be addressed in a straightforward fashion. By “straightforward” I don’t mean the criticisms could be addressed easily–collecting diet data for dozens of species in a community is not easy! Rather, I mean it was obvious what sort of new data were needed, and how to obtain them (it was just a lot of work to obtain them). So that addressing the criticisms appeared to many as a really good research opportunity. Criticisms of early observational studies of biodiversity-ecosystem function relationships as confounded by sampling effects were seen in much the same way, I think. People quickly realized how to address the criticisms with new experimental designs and statistical analyses, and so addressing them was seen as a research opportunity. In contrast, when I suggest (as I did at the end of Fox 2012) that the time is ripe for a new generation of work on disturbance-diversity relationships, grounded in modern coexistence theory, it’s not immediately obvious exactly what sort of work that would involve. “Go out and test for storage effects and relative nonlinearity, and see how their strength varies as a function of disturbance frequency and intensity” isn’t straightforward in the way that “go out and assess the diets of every species in a community” is. Or at least, it probably doesn’t seem that way to most people. Put slightly differently, I suspect that calls from Gary Polis and others for better food web data, or calls to address the issue of sampling effects in BD-EF research, sounded to many people like calls to continue the same research programs by different means. While I suspect my call for research on disturbance-diversity relationships to be based on modern coexistence theory rather than the IDH probably sounds to a lot of people like an attempt to change the question, and thus to replace an existing research program with a new (and not clearly-defined) one. Or perhaps I’m wrong, perhaps it’s only with the benefit of hindsight (and perhaps only to my eyes?) that the history of food web research looks like a single continuous research program with a healthy back-and-forth between theory and data? Perhaps at the time, and to those involved, the critiques of Polis and others felt like calls to replace one (in their view failed) research program with an alternative program? I don’t know, just speculating here, comments welcome.

28 thoughts on “Are there Buddy Holly ideas? (or, has any line of ecological or evolutionary research ever been prematurely abandoned?) (UPDATE)

  1. So I think this is an interesting idea, but one that is really hard to evaluate due to a bias in the data. In order to identify an idea that was proposed and later abandoned prematurely, you need to be aware of it and also be able to judge its worth. There are a number of ways you probably would not be aware of these “great, but perhaps before their time” ideas.

    1) The idea was proposed by a student, was rejected by their committee or adviser, and then never even submitted. It could be later published (or not) by a different research group.
    2) The idea was submitted but then never accepted for publication because of push back from journals or reviewers. It could be later published (or not) by a different research group.
    3) The idea was published, criticized, and abandoned…. and is yet to be taken back up by another scientist.

    In the first two cases its obvious why you would not be aware of those ideas. There are probably lots of examples of a student having a novel, good idea, getting discouraged and dropping it, only to later see someone else publish those ideas years later. From our outside perspective, those ideas (if published) would appear to have never been proposed and then abandoned, only the original proposers would know that it was not the first time the idea had been proposed. If the ideas have yet to be published there is no way to get a count on them.

    In the third case, if the idea has not come back around again and been accepted we’d have little interest in reading some old “discredited” line of research because, again, the community is not yet aware of the value of the original idea.

    Given the issues above, I think getting a firm grip on the number of “Buddy Holly” ideas that have been proposed would be quite difficult, but I’m sure that if we accept the three scenarios above as fitting the category then your post underestimates how common this might be.


    • Your categories 1 and 2 are different than what I intended. They’re good ideas that never got off the ground in the first place. Analogous to an excellent musician who remains undiscovered.

      We might call such ideas Mendel ideas, since Mendel’s ideas remained obscure when he published them and were only rediscovered and recognized as valuable much later. πŸ™‚

      • Ah I see. So you meant specifically things that made “prime time” in the scientific community but then were prematurely abandoned. Yes, I agree that this would be a fairly small group of topics. Its not often that a good idea would get out into the community and then have everyone push back against it. Normally we get something like a huge debate, like the trophic cascade story or the SLOSS debates.

  2. OK, I’ll bite, but the following statements are entirely research-free, as Dave Barry might say. How about the inheritance of quantitative traits, i.e. “blending” inheritance? This was a big part of Darwin’s thinking, but when Mendel’s work was rediscovered around 1900, wasn’t there a shift toward greater emphasis on the importance of more qualitative/dichotomous inheritance patterns? And later, both types were shown to be manifestations of a single process, as greater understandings of the mechanisms of inheritance (esp chromosomes), and then gene molecular structure, were realized?

    I agree that maternal/paternal inheritance/effects, e.g mitochondrial/plastid inheritance etc., are not at all in the same class as Lamarck’s ideas. Very different in fact.

    However, research on Bigfoot should never ever be abandoned, let’s get that straight right now. He/she/it has been seen on several TV commercials recently, and doing some damage too. Actually Reinhold Messner, the famous mountaineer, actually wrote a pretty decent book on the possibility of a Yeti-like creature inhabiting the more remote parts of the Himalayas.

    • Hmm, interesting suggestion, but I don’t know that Darwin’s ideas about inheritance qualify as Buddy Holly ideas. The biometricians never gave up on describing the inheritance of quantitative variation or emphasizing its importance. Everyone did give up on Darwin’s idea about the underlying mechanism of inheritance (“gemmules” carried in the blood, if memory serves). But as far as I know that was for good reason–data from transfusion experiments falsified the idea, and it was never revived.

      Although you’re right that there was a brief span of time when Mendelism was seen by some as an alternative to Darwinism (and not just Darwin’s ideas about inheritance, but his ideas about evolution by natural selection). That was part of the “eclipse of Darwinism” in the late 19th and early 20th centuries.

    • You must be mistaken, Jim. Bigfoot research is more productive than its ever been!

      A great article on Sasquach distributions was published tin the Journal of Biogeography only a few years ago:

      Lozier JD, Aniello P, Hickerson MJ. 2009. Predicting the distribution of Sasquatch in western North America: anything goes with ecological niche modelling. Journal of Biogeography, 36, 1623-1627.
      Here’s the PDF

  3. You had me at group selection. The reasons it was (is?) dismissed by nearly a whole generation of biologists were more about dogmatism than science. Clearly, there hasn’t been enough work on the question to entirely dismiss it as many people have. I’ve spent so much time listening to social insect biologists discussing the evolution of social behavior, and the talk about group selection is often, well, inadequately skeptical because it doesn’t involve data. And the responses to Wilson’s latest salvos have defended kin selection rather than evaluating group selection.

    • It’s interesting to speculate on whether Buddy Holly ideas tend to be certain sorts of ideas. Perhaps ideas that hinge crucially on conceptual/philosophical issues that can’t really be settled by data? Perhaps philosophical issues and ideas are the ones that are most susceptible both to being killed off, and to being subsequently revived? In other words, philosophical fashions can wax, wane, and wax again, like clothing fashions?

    • My understanding (as a recent undergrad who worked in a sociobiology lab on a theoretical project) is that, while the old group selection models have since been acknowledged as problematic, most sociobiologists agree that inclusive fitness theory and more recent multi-level selection theory are mathematical equivalent (Hamilton 1975, Queller 1992, Wade et al. 2009, Marshall 2011), two different ways of looking which can be translated from one to the other, both being partitions of the Price Equation, though there remains many misconceptions and semantic issues. From D.S. Wilson “Clash of Paradigms”, “I count myself among them as a proponent of MLST who acknowledges the utility of IFT, along with David Queller, a proponent of IFT who acknowledges the utility of MLST.”

      However, while *theoretically* equivalent, which perspective is better in practice depends a lot on the types of questions being asked, the model system, and historical successes–for example, IFT has been much more successful in explaining phenomena in social insect biology than MLST has been, probably for both real practical reasons (it’s hard to measure groups) but also the historical popularity of IFT.

      As per E.O. Wilson’s recent remarks, a lot of the criticism concerned what seemed to be his downplaying of the success of the IFT literature, and his misconceptions of both IFT and recent MLST–his version of group selection is more reminiscent of the outdated models.

      Also, there are some who have proposed more substantiated challenges, mostly mathematical to the supposed equivalence between IFT and MLST (see Traulsen 2009, Veelen et al. 2010). I think there are problems with the sometimes informal use of IFT in experiments, and that there remains many theoretical and mathematical issues to understanding social evolution, which in turn have not been well explored experimentally (e.g. the role of stochasticity/drift/fixation probabilities).

  4. Ooh, here’s a Buddy Holly candidate: Bayes’ Theorem as a statistical/inferential tool. Although I don’t know enough about the history of statistics to say if it was promising/successful but then killed off by Fisher/Neyman/Pearson. Or if it’s more of an idea that just had a long “lag phase” before taking off in the past few decades.

    • I thought we were restricted to ecology and evolution topics. If we’re going to include all of science then there are some really good candidates. The concept of greenhouse gases affecting the climate (Tyndall, Arrhenius) for example, which was ignored for a long time after first proposed by Tyndall and Fourier.

      • I’m broadening it since we don’t seem to be getting many comments. πŸ™‚

        Was the greenhouse effect something that was actively taken up for a while but then abandoned before it should’ve been? Or was it another one of these long lag-phase ideas that was out there for a long time before getting taken up in a big way? Such ideas are of course an interesting topic in themselves, but that’d have to be another post.

      • Yes, I’m pretty sure it meets your criteria, two different times in fact, but will check. There was a long gap between Tyndall’s fairly definitive radiation balance measurements of various trace gases (1859) and Arrhenius’ late 19th C work that gave the first quantitative estimates of trace gas concentration effects on temperature, and then another one between Arrehenius’ work and Callendar (in the 1930s/1940s), and you could perhaps even argue that there was a third one between then and the 1950s.

  5. Neutral theory – Caswell had an enormous amount of the theory worked out in 1976, then it got ignored (despite being a great – superior? – null model than the ones then current). THen in the span of two years Bell and Hubbell their paper and book and it was all the rage.

    Can something go from being a Buddy Holly idea to a bandwagon?

    I would even argue r/K selection. It got a pretty good look the first time around but then it was pretty much verboten for a long time. But it keeps coming back in different guises like fast vs slow lifestyles (justifiably so in my opinion). There’s no doubt it deserved a pruning and push for precision the first time around, but the way it was completely cut off was excessive.

    In general makes me wonder if there isn’t a propensity for things to be (or us to perceive) things as Buddy Holly or bandwagon and never have Goldilocks ideas that get just the right amount of attention?

    • Caswell’s version of neutral theory is another example of an idea that maybe should’ve taken off but didn’t. Like an undiscovered musical genius (EDIT: “undiscovered” is a poor choice of words here, since Caswell’s theory was published in a prominent venue. Caswell’s version of neutral theory is more like a one-hit wonder than a totally undiscovered musician). Or like a mutation that’s favored by selection but yet happens to get lost to drift. Not an idea that was popular/productive but yet got killed off by criticism even though it didn’t deserve to die.

      In principle, I don’t see why an idea couldn’t go from being a Buddy Holly idea to being a bandwagon.

      Your suggestion of r/K selection is a really good one. I don’t know the history well (you’d know it better than I would, I’m sure). But yeah, based on what I know I think you’re right that it was a popular idea that came in for some deserved criticism, and the mark got overshot and it became verboten. So yeah, probably a Buddy Holly idea. Although an interesting wrinkle there is that, in the minds of people outside of life history theory, I don’t think the idea was ever killed off. It lived on in places like undergrad ecology textbooks and in the backs of the minds of people who work on other topics.

      • Brian, you hit the nail on the head for me when you suggested r/K selection as an idea that went from meteoric in interest to ignored in rapid order. My dissertation research on life-history was inspired by Otto Solbrig’s r/K ideas related to dandelions, so I studied it all pretty closely at the time (this all played out in the 70s as I recall). There were other ideas like the guerilla-phalanx distinction that similarly became viewed as being overly simplistic and only briefly considered.

        I view the difficulties faced by both of these (and many other) ideas as a common problem: nature is a complex system – there are several different types of selective environments that can support a variety of life-history tradeoffs involving such things as reproductive effort and survival/competitive ability. So, if you are looking to nature for examples of r/K selection, you can use a broad-beam searchlight approach and count every comparison that looks like it could be an example of r- vs. K-selection (which is what a lot of people were doing). If you look more carefully, you can focus on exceptions and find plenty of cases where very different selection processes are leading to somewhat similar life-history trait dichotomies (which is what some other folks did).

        In the case of r/K selection there was no persistent champion of the general idea, so it became used largely in theoretical circles where one could invoke it as a simple dichotomy. If we take similar but only slightly more complex ideas that rapidly followed, such as Grime’s RCS theory and his related Hump-Backed Model or Huston’s Dynamic Equilibrium Model, those ideas are still very prominently discussed because they have dedicated champions, not because they don’t suffer from the same difficulties. The Intermediate Disturbance Hypothesis is somewhere in between – there are supporters out there, but they are not so dedicated to the task of defending the idea as are certain defenders of other ideas.

        Great topic for further discussion.

      • Very interesting thoughts Jim.

        Re: some ideas persisting because they have dedicated champions, yup. That’s kind of the flip side of something I discussed in an old post on why some ecological ideas are controversial but others aren’t: I suggested that prominent individuals have some limited ability to create controversy where none would otherwise exist. The flip side of that is that prominent individuals also have some limited ability to sustain ideas in the face of controversy, if not suppress controversy. Which I think is unfortunate, even though I’m sure that at this point it works in this blog’s favor.

        Re: your analogy to a broad vs. narrow-beam “searchlight” when looking for evidence for some hypothesized phenomenon, I think that’s a very good and important point. Will have to think more about that with an eye towards maybe posting something in future.

  6. How about Goldschmidt’s early concept of radical genetic changes causing ontogenetic changes leading to quick speciation events? Was that ignored for a while and then confirmed by things like discovery of homeobox genes and their mutations?

  7. I love the concept of Buddy Holly Ideas. I can’t think of any right now, but the question is hard, and reminds me of my job interview with Mark Westoby back when I was just finishing my BSc(hons) in Wellington. Mark’s question was along the lines of: “so, from your knowledge of the literature [hons student internally cries], what ideas do you think have been researched to the point where we know the answer, and it’s not interesting to keep working on them, and what areas do you think are important for us to address in the future”. Tangential comment, I know…but I guess my point is that there’s another sort of idea for your taxonomy of science – the “done to death idea” [no clever ideas for a name right now either!].

  8. While I don’t agree with all of their propositions, a lot of the conceptual work on ecosystem development by the Odum brothers, Ulanowicz, Finn, and even Margalef made some interesting quantitative predictions that couldn’t be robustly-tested at the time. I think a lot of their insights were abandoned due to some of the more “out-there” ecosystems-as-deterministic-meta-organisms stuff being proposed by some of the aforementioned. Much of it seems to have subsequently been ignored by everyone except Michel Loreau. Maybe NEON’s massive infrastructure can begin to confront some of these predictions with data. I know, however, that there are a large number of ecosystem ecologists that wouldn’t touch this stuff with a ten-foot-pole!

    Ecological stoichiometry is another one I think needs more attention, but there are a few big, fancy labs that appear to be working on this kind of stuff.

    • Interesting comments. Re: Odum & Odum-Ulanowicz-Finn-style ecosystem ecology, that’s certainly a research program that’s been at least partially abandoned, in the sense that it’s less influential and probably has fewer adherents than it used to have. And I think you’re right about the reasons why many folks shied away from it (and about how Michel Loreau is probably the person who’s done the most to try to “translate” that stuff into viable population ecology terms). So I guess whether you regard those as Buddy Holly ideas depends on whether you see Michel Loreau’s work as demonstrating the value of continuing to pursue those ideas, despite the many criticisms to which those ideas were subjected. I could imagine arguing that either way.

      Something similar might be said of the “hierarchy theory” approach to ecology (Allen, Starr, and others), except that off the top of my head I don’t know that anyone’s had any success “translating” those ideas into a more “mainstream” framework (if that’s the right word).

      • Interesting suggestion about the Ulanowicz/Odum programme. Two opposing views on why it appears less popular now.

        First, one might claim that although those ideas have been around in some form for a long time (at least since Lotka and Tansley, and perhaps since Boltzmann), nobody has yet come up with a very clear argument about why they must be true, and there’s little empirical evidence that they are true. Lotka’s work on this looks to me as though it was explicitly modelled on Darwin, and yet there are huge gaps in the logic that haven’t yet been filled. There’s an entertaining section on empirical evidence in the second episode of the BBC documentary series “All watched over by machines of loving grace”. The episode is called “The use and abuse of vegetational concepts” (seems to be available on the web, but not sure if legitimately).

        Second, it may be that ecosystem ecology and community ecology have diverged much further than they had in the 60s and early 70s. Thus, conceptual work on ecosystem ecology may be just as lively as it was back then, but most community ecologists don’t know about it. Maybe partly because ecosystem ecology has been largely ignored by influential textbooks. May’s “Stability and complexity in model ecosystems” surprisingly says almost nothing about ecosystems. I recall it being pointed out to me as an undergraduate that the first edition of Begon, Harper and Townsend mentioned the word “ecosystem” exactly once. I no longer have an early edition to check whether this is actually true, and there is more about ecosystems in more recent editions.

        There are papers that bridge the gap between community and ecosystem ecology (e.g., Ulanowicz, Holt and Barfield 2014, Ecology Letters 17:127-136). It still seems possible that there is a really great theory of ecosystem ecology waiting to emerge.

  9. Hi Jeremy

    It’s a bit of a tangent, but let me float the idea anyway as 1) it addresses your “point 1”, 2) it may help clarify where your zombies come from and 3) I enjoy the mixed metaphors.

    I suggest a precise link between which aspects of your IDH (i.e. in your broad sense, not Connell’s) are zombies and the topic of sloppy imprecise citation as raised in your previous post. People have cited Connell 1978 (and many others) for the IDH without pausing to check what was and wasn’t stated … and the key concepts have lost precision in significant portion of the resulting literature. The fuzziness allowed add-ons that then evolved its own arms and legs (at least in some of the literature, including the text books that you have mentioned previously, so it became relatively “mainstream”). My suggestion would be that if we go back to check what Connell 1978 wrote it remains reasonable. Thus your zombie and Connell’s baby should be seen as separate entities even if both appear to sit in the same bath tub.

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