Reproducibility: Which Levers?

I was reading about health behavior change today and I was reminded that there is a difference between a complicated system and a complex system (D.T. Finegold and colleagues) and it crystalized for me why  the confident pronouncements of the reproducibility folks strike me as earnest but often misguided. If you think about it, most laboratory experiments are complicated systems that are meant to be roughly linear: There may be a lot of variables and many people involved in the manipulation or measurement of those variables but ultimately those manipulations and measurements should lead to observed changes in the dependent variable and then there is a conclusion; by linear system I mean that these different levels of the experiment are not supposed to contaminate each other. There are strict rules and procedures, context-specific of course, for carrying out the experiment and all the people involved need to be well trained in those procedures and they must follow the rules for the experiment to have integrity. Science itself is another matter altogether. It is a messy nonlinear dynamic complex system from which many good and some astounding results emerge, not because all the parts are perfect, but in spite of all the imperfection and possibly because of it. Shiffren, Börner and Stigler (2018) have produced a beautiful long read that describes this process of “progress despite irreproducibility.” I will leave it to them to explain it since they do it so well.

I am certain that the funders and the proponents of all the proposals to improve science are completely sincere but we all know that the road to hell is paved with good intentions. The reason that the best intentions are not going to work well in this case is that the irreproducibility folks are trying to “fix” a complex system by treating it as if it is a complicated problem. Chris Chambers tells a relatively simple tale in which a journal rejects a paper (according to his account) because a negative result was reported honestly which suggests that a focus on positive results rewards cheating to get those results and voilà: the solution is to encourage publication without the results. This idea is fleshed out by Nosek et al (2018) in a grand vision of a “preregistration revolution” which cannot possibly be implemented as imagined or result in the conceived outcomes. All possible objections have been declared to be false (bold print by Chris Chambers) and thus they have no need of my opinion. I am old enough to be starting my last cohort of students so I have just enough time to watch them to get tangled up in it. I am a patient person. I can wait to see what happens (although curiously no objective markers of the success of this revolution have been definitively put forward).

But here’s the thing. When you are predicting the future you can only look to the past. So here are the other things that I read today that lead me to be quite confident that although science will keep improving itself as it always has done, at least some of this current revolution will end up in the dust. First, on the topic of cheating, there is quite a big literature on academic cheating by undergraduate students which is directly relevant to the reproducibility movement. You will not be surprised to learn that (perceived) cheating is contagious. It is hard to know the causal direction – it is probably reciprocal. If a student believes that everyone is cheating the likelihood that the student will cheat is increased. Students who cheat believe that everyone else is cheating regardless of the actual rate of cheating. Students and athletes who are intrinsically versus extrinsically motivated are also less likely to cheat so it is not a good idea to undermine intrinsic motivation with excessive extrinsic reward systems, especially those that reduce perceived autonomy. Cheating is reduced by “creating a deeply embedded culture of integrity:” Culture is the important word here because most research and most interventions target individuals but it is culture and systems that need to be changed. Accomplishing a culture of integrity includes (perhaps you will think paradoxically) creating a trusting and supportive atmosphere with reduced competitive pressures while ensuring harsh and predictable consequences for cheating. The reproducibility movement has taken the path of deliberately inflating the statistics on the prevalence of questionable research practices with the goal of manufacturing a crisis, under the mistaken belief that the crisis narrative is necessary to motivate change when it is more likely that this narrative will actually increase cynicism and mistrust, having exactly the opposite effect.

The second article I read that was serendipitously relevant was about political polarization. Interestingly, it turns out that perceived polarization reduces trust in government whereas actual polarization between groups is not predictive of trust, political participation and so on. It is very clear to me that the proponents of this movement are deliberately polarizing and have been since the beginning, setting hard scientists against soft, men against woman and especially the young against the old (I would point to parts of my twitter feed as proof of this I but I don’t need to contaminate your day with that much negativity, suffice to say it is not a trusting and supportive atmosphere). The Pew Center shows that despite decades of a “war against science” we remain one of the most trusted groups in society. It is madness to destroy ourselves from within.

A really super interesting event that happened in my tweet feed today was the release of the report detailing the complete failure of the Gates Foundation $600M effort to improve education by waving sticks and carrots over teachers with the assumption that getting rid of bad teachers was a primary “lever” that when pulled would spit better educated minority students out the other end (seriously, they use the word levers, it cracks me up; talk about mistaking a complex system for a complicated one). Anyway, it didn’t work. The report properly points out that that the disappointing results may have occurred because their “theory of action” was wrong. There just wasn’t enough variability in teacher quality even at the outset for all that focus on teacher quality to make that much difference especially since the comparison schools were engaged in continuous improvement in teacher quality as well. But of course the response on twitter today has been focused on teacher quality: many observers figure that the bad teachers foiled the attempt through resistance, of course! The thing is that education is one of those systems in our society that actually works really well, kind of like science. If you start with the assumption that that the scientists are the problem and if you could just get someone to force them to shape up (see daydream in this blog by Lakens in which he shows that he knows nothing about professional associations despite his excellence as a statistician)…well, I think we have another case of people with money pulling on levers with no clue what is behind them.

And finally, let’s end with the Toronto Star, an excellent newspaper, that has a really long read (sorry, its long but really worth your time) describing a dramatic but successful change in a nursing home for people with dementia. It starts out as a terrible home for people with dementia and becomes a place you would (sadly but confidently) place your family member. This story is interesting because you start with the sense that everyone must have the worst motives in order for this place to be this bad—care-givers, families, funders, government—and end up realizing that everyone had absolutely the best intentions and cared deeply for the welfare of the patients. The problem was an attempt to manage the risk of error and place that goal above all others. You will see that the result of efforts to control error from the top down created the hell that the road paved with good intentions must inevitably create.

So this is it, I may be wrong and if I am it will not be the first time. But I do not think that scientists have been wasting their time for the last 30 years as one young person declared so dramatically in my twitter feed. I don’t think that they will waste the next 30 years either because they will mostly keep their eye on whatever it is that motivated them to get into this crazy business. Best we support and help each other and let each other know when we have improved something but at the same time not get too caught up in trying to control what everyone else is doing. Unless of course you are so disheartened with science you would rather give it up and join the folks in the expense account department.

Post-script on July 7, 2018: Another paper to add to this grab-bag:

Kaufman, J. C., & Glǎveanu, V. P. (2018). The Road to Uncreative Science Is Paved With Good Intentions: Ideas, Implementations, and Uneasy Balances. Perspectives on Psychological Science, 13(4), 457-465. doi:10.1177/1745691617753947

I liked this perspective on science:

“The propulsion model is concerned with how a creative work affects the field. Some types of contributions stay within the existing paradigm. Replications,1 at the most basic level, aim to reproduce or recreate a past successful creation, whereas redefinitions take a new perspective on existing work. Forward or advance forward incrementations push the field ahead slightly or a great deal, respectively. Forward incrementations anticipate where the field is heading and are often quite successful, whereas advance forward incrementations may be ahead of their time and may be recognized only retrospectively. These categories stay within the existing paradigm; others push the boundaries. Redirections, for example, try to change the way a field is moving and ake it in a new direction. Integrations aim to merge two fields, whereas reinitiation contributions seek to entirely reinvent what constitutes the field.”

 

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Reproducibility: Solutions (not)

Let’s go back to the topic of climate change since BishopBlog started this series of blogposts off by suggesting that scientists who question the size of the reproducibility crisis are playing a role akin to climate change deniers, by analogy with Orestes and Conway’s argument in Merchants of Doubt. While some corporate actors have funded doubting groups in an effort to protect their profits, as I discussed in my previous blogpost, others have capitalized on the climate crisis to advance their own interests. Lyme disease is an interesting case study in which public concern about climate change gets spun into a business opportunity, like this: climate change → increased ticks → increased risk of tick bites → more people with common symptoms including fever and fatigue and headaches → that add up to Chronic Lyme Disease Complex → need for repeated applications of expensive treatments → such as for example chelation because heavy metals toxicities. If I lost you on that last link, well, that’s because you are a scientist. But nonscientists like Canadian Members of Parliament got drawn into this and now a federal framework to manage Lyme Disease is under development because the number of cases almost tripled over the past five years to, get this, not quite 1000 cases (confirmed and probable). The trick here is that if any one of the links seems strong to you the rest of the links shimmer into focus like the mirage that they are. And before you can blink, individually and collectively, we are hooked into costly treatments that have little evidence of benefits and tenuous links to the supposed cause of the crisis.

The “science in crisis” narrative has a similar structure with increasingly tenuous links as you work your way along the chain: pressures to publish → questionable research practices → excessive number of false positive findings published → {proposed solution} → {insert grandiose claims for magic outcomes here}. I think that all of us in academia at every level will agree that the pressures to publish are acute. Public funding of universities has declined in the U.K., the U.S. and in Canada and I am sure in many other countries as well. Therefore the competition for students and research dollars is extremely high and governments have even made what little funding there is contingent upon the attraction of those research dollars. Subsequently there is overt pressure on each professor to publish a lot (my annual salary increase is partially dependent upon my publication rate for example). Furthermore, pressure has been introduced by deliberately creating a gradient of extreme inequality among academics so that expectations for students and early career researchers are currently unrealistically high. So the first link is solid.

The second link is a hypothesis for which there is some support although it is shaky in my opinion due to the indirect nature of the evidence. Nonetheless, it is there. Chris Chambers tells this curious story where, at the age of 22 and continuing forward, he is almost comically enraged that top journals will not accept work that is good quality because the outcome was not “important” or “interesting.” And yet there are many lesser tier journals that will accept such work and many researchers have made a fine career publishing in them until such time as they were lucky enough to happen upon whatever it was that they devoted their career to finding out. The idea that luck, persistence and a lifetime of subject knowledge should determine which papers get into the “top journals” seems right to me. There is a problem when papers get into top journals only because they are momentarily attention-grabbing but that is another issue. If scientists are tempted to cheat to get their papers in those journals before their time they have only themselves to blame. One big cause of “accidental” findings that end up published in top or middling journals seems to be low power however, which can lead to all kinds of anomalous outcomes that later turn out to be unreliable. Why are so many studies underpowered? Those pressures to publish play a role as it is possible to publish many small studies rather than one big one (although curiously it is reported that publication rates have not changed in decades after co-authorship is controlled even though it seems undeniable that the pressure to publish has increased in recent times). Second, research grants are chronically too small for the proposed projects. And those grants are especially too small for woman and in fields of study that are quite frankly gendered. In Canada this can be seen in a study of grant sizes within the Natural Sciences and Engineering Research Council and by comparing the proportionately greater size of cuts to the Social Sciences and Humanities Research Council.

So now we get to the next two links in the chain. I will focus on one of the proposed solutions to the “reproducibility crisis” in this blog and come back to others in future posts. There is a lot of concern about too many false positives published in the literature (I am going to let go the question about whether this is an actual crisis or not for the time being and skip to the next link, solutions for that problem). Let’s start with the suggestion that scientists dispense with the standard alpha level of .05 for significance and replace it with p < .005 which was declared recently by a journalist (I hope the journalist and not the scientists in question) to be a raised standard for statistical significance. An alpha level is not a standard. It is a way of indicating where you think the balance should be between Type I and Type II error. But in any case, the proposed solution is essentially a semantic change. If a study yields a p-value between .05 and .005 the researcher can say that the result is “suggestive” and if it is below .005 the researcher can say that it is significant according to this proposal. The authors say that further evidence would need to accumulate to support suggestive findings but of course further evidence would need to accumulate to confirm the suggestive and the significant findings (it is possible to get small p values with an underpowered study and I thought the whole point of this crisis narrative was to get more replications!). However, with this proposal the idea seems to be to encourage studies to have a sample size 70% larger than is currently the norm. This cost is said to be offset by the benefits, but, as Timothy Bates points out, there is no serious cost-benefit analysis in their paper. And this brings me to the last link. This solution is proposed as a way of reducing false positives markedly which in turn will increase the likelihood that published findings will be reproducible. And if everyone magically found 70% more research funds this is possibly true. But where is the evidence that the crisis in science, whatever that is, would be solved? It is the magic in the final link that we really need to focus on.

I am a health care researcher so it is a reflex for me to look at a proposed cure and ask two questions (1) does the cure target the known cause of the problem? (2) is the cure problem-specific or is it a cure-all? Here we have a situation where the causal chain involves a known distal cause (pressure to publish) and known proximal cause (low power). The proposed solution (rename findings with p between .05 to .005 suggestive) does not target either of these causes. It does not help to change the research environment in such a way as to relieve the pressure to publish or to help researchers obtain the resources that would permit properly powered studies (interestingly the funders of the Open Science Collaborative have enough financial and political power to influence the system of public pensions in the United States and therefore, improving the way that research is funded and increasing job stability for academics are both goals within their means but not, as far as I can see, goals of this project). Quite the opposite in fact because this proposal is more likely to increase competition and inequality between scientists than to relieve those pressures and therefore the benefits that emerge in computer modeling could well be outweighed by the costs in actual application. Secondly, the proposed solution is not “fit for purpose”. It is an arbitrary catch-all solution that is not related to the research goals in any one field of study or research context.

That does not mean that we should do nothing and that there are no ways to improve science. Scientists are creative people and each in their own ponds have been solving problems long before these current efforts came into view. However, recent efforts that seem worthwhile to me and that directly target the issue of power (in study design) recognize the reality that those of us who research typical and atypical development in children are not likely to ever have resources to increase our sample sizes by 70%. So, three examples of helpful initiatives:

First, efforts to pull samples together through collaboration are extremely important. One that is fully on-board with the reproducibility project is of course the ManyBabies initiative. I think that this one is excellent. It takes place in the context of a field of study in which labs have always been informally  inter-connected not only because of shared interests but because of the nature of the training and interpersonal skills that are required to run those studies. Like all fields of research there has been some partisanship (I will come back to this because it is a necessary part of science) but also a lot of collaboration and cross-lab replication of studies in this field for decades now. The effort to formalize the replications and pool data is one I fully support.

Second, there have been ongoing and repeated efforts by statisticians and methodologists to teach researchers how to do simple things that improve their research. Altman sadly died this week. I have a huge collection of his wonderful papers on my hard-drive for sharing with colleagues and students who surprise me with questions like How to randomize? The series of papers by Cumming and Finch on effect sizes along with helpful spreadsheets are invaluable (although it is important to not be overly impressed by large effect sizes in underpowered studies!). My most recent favorite paper describes how to chart individual data points, really important in a field such as ours in which we so often study small samples of children with rare diagnoses. I have an example of this simple technique elsewhere on my blog. If we are going to end up calling all of our research exploratory and suggestive now (which is where we are headed, and quite frankly a lot of published research in speech-language pathology has been called that all along without ever getting to the next step), let’s at least describe those data in a useful fashion.

Third, if I may say so myself, my own effort to promote the N-of-1 randomized control design is a serious effort to improve the internal validity of single case research for researchers who, for many reasons, will not be able to amass large samples.

In the meantime, for those people suggesting the p < .005 thing, it seems irresponsible to me for any scientist to make a claim such as “reducing the P-value threshold for claims of new discoveries to 0.005 is an actionable step that will immediately improve reproducibility” on the basis of a little bit of computer modeling, some sciencey looking charts with numbers on them and not much more thought than that.  I come back to the point I made in my first blog on the reproducibility crisis and that is that if we are going to improve science we need to approach the problem like scientists. Science requires clear thinking about theory (causal models), the relationship between theory and reality, and evidence to support all the links in the chain.

Reproducibility: On the Nature of Scientific Consensus

The idea that scientists who raise questions about whether (ir)reproducibility is a crisis or not are like the “merchants of doubt” is argued via analogy with, for example, climate change deniers. It’s a multistep analogy. First there is an iron-clad consensus on the part of scientists that humans are causing a change in the climate that will have catastrophic consequences. Because the solutions to the problem threaten corporate interests, those big money interests astroturf groups like “Friends of Science” to sow doubt about the scientific consensus in order to derail the implementation of positive policy options. For the analogy on Bishop’s Blog to work, there must first be a consensus among scientists that the publication of irreproducible research is a crisis, a catastrophe even. I am going to talk about this issue of consensus today although it would be more fun to follow that analogy along and try to figure out whether corporate interests are threatened by more or less scientific credibility and how the analogy works when it is corporate money that is funding the consensus and not the dissenters! But anyway, on the topic of consensus…

The promoters of the reproducibility crisis have taken to simply stating that there is a consensus, citing most frequently a highly unscientific Nature poll. I know how to create scientific questionnaires (it used to be part of my job in another life before academia) and it is clear that the question “Is there a reproducibility crisis?” with the options “crisis,” “slight crisis” (an oxymoron) and “no crisis” is a push poll. The survey was designed to make it possible for people to claim “90% of respondents to a recent survey in Nature agreed that there is a reproducibility crisis” which is how you sell toothpaste, not determine whether there is a crisis or not. On twitter I have been informed, with no embarrassment, that unscientific polls are justified because they are used to “raise awareness”. The problem comes when polls that are used to create a consensus are also used as proof of that consensus. How does scientific consensus usually come about?

In many areas of science it is not typical for groups of scientists to formally declare a consensus about a scientific question but when there are public or health policy implications working groups will create consensus documents, always starting with a rigorous procedure for identifying the working group, the literature or empirical evidence that will be considered, the standards by which that evidence will be judged and the process by which the consensus will emerge. Ideally it is a dynamic and broad based exercise. The Intergovernmental Panel on Climate Change is a model in this regard and it is the rigorous nature of this process that allows us to place our trust in the consensus conclusion even when we are not experts in the area of climate. A less complex and for us more comprehensible example is the recent process employed by the CATALISE consortium to propose that Specific Language Impairment be reconceptualised as Developmental Language Disorder. This process meets all the requirements of a rigorous process with the online Delphi technique an intriguing part of the series of events that led to a set of consensus statements about the identification and classification of developmental language disorders. Ultimately each statement is supported by a rationale from the consortium members including scientific evidence when available. The consortium itself was broad based and the process permitted a full exposition of points of agreement and disagreement and needs for further research. For me, importantly, a logical sequence of events and statements is involved-the assertion that the new term be used was the end of the process, not the beginning of it. The field of speech-language pathology as a whole has responded enthusiastically even though there are financial disincentives to adopting all of the recommendations in some jurisdictions. Certainly the process of raising awareness of the consensus documents has had no need of push polls or bullying. One reason that the process was so well received, beyond respect for the actors and the process, is that the empirical support for some of the key ideas seems unassailable. Not everyone agrees on every point and we are all uncomfortable with the scourge of low powered studies in speech and language disorders (an inevitable side effect of funder neglect); however, the scientific foundation for the assertion that language impairments are not specific has reached a critical mass, and therefore no-one needs to go about beating up any “merchants of doubt” on this one. We trust that in those cases where the new approach is not adopted it is generally due to factors outside the control of the individual clinician.

The CATALISE process remains extraordinary however. More typically a consensus emerges in our field almost imperceptibly and without clear rationale. When I was a student in 1975 I was taught that children with “articulation disorders” did not have underlying speech perception deficits and therefore it would be a waste of time to implement any speech perception training procedures (full stop!). When I began to practice I had reason to question this conclusion (some things you really can see with your own eyes) so I drove into the university library (I was working far away in a rural area) and started to look stuff up. Imagine my surprise when I found that the one study cited to support this assertion involved four children who did not receive a single assessment of their speech perception skills (weird but true). Furthermore there was a long history of studies showing that children with speech sound disorders had difficulties with speech discrimination. I show just a few of these in the chart below (I heard via Twitter that, at the SPA conference just this month in Australia, Lise Baker and her students reported that 83% of all studies that have looked at this question found that children with a speech sound disorder have difficulties with speech perception). So, why was there this period from approximately 1975 through about 1995 when it was common knowledge that these kids had no difficulty with speech perception? In fact some textbooks still say this. Where did this mistaken consensus come from?

When I first found out that this mistaken consensus was contrary to the published evidence I was quite frankly incandescent with rage! I was young and naïve and I couldn’t believe I had been taught wrong stuff. But interestingly the changes in what people believed to be true were based on changes in the underlying theory which is changing all the time. In the chart below I have put the theories and the studies alongside each other in time. Notice that the McReynolds, Kohn, and Williams (1975) paper which found poorer speech perception among the SSD kids, actually concluded that they didn’t, contrary to their own data but consistent with the prevailing theory at the time!

History of Speech Perception Research

What we see is that in the fifties and sixties, when it was commonly assumed that higher level language problems were caused by impairments in lower level functions, many studies were conducted to prove this theory and in fact they found evidence to support that theory with some exceptions. In the later sixties and seventies a number of theories were in play that placed strong emphasis on innate mechanisms. There were few if any  studies conducted to examine the perceptual abilities of children with speech sound disorders because everyone just assumed they had to be normal on the basis of the burgeoning field of infant perceptual research showing that neonates could perceive anything (not exactly true but close enough for people to get a little over enthusiastic). More recently emergentist approaches have taken hold and more sophisticated techniques for testing speech perception have allowed us to determine how children perceive speech and when they will have difficulty perceiving it. The old theories have been proved wrong (not everyone will agree on this because the ideas about lower level sensory or motor deficits are zombies; the innate feature detector idea, that is completely dead; for the most part, the evidence is overwhelming and we have moved on to theories that are considerably more complex and interesting, so much so that I refer you to my book rather than trying to explain them here).

The question is, on the topic of reproducibility, whether it would have been or would be worthwhile for anyone to try and reproduce, let’s say Kronvall and Diehl (1952) just for kicks? No! That would be a serious waste of time as my master’s thesis supervisor explained to me in the eighties when he dragged me more-or-less kicking and screaming into a room with a house-sized vax computer to learn how to synthesize speech (I believe I am the first person to synthesize words with fricatives, it took me over a year). It is hard to assess the clinical impact of all that fuzzy thinking through the period 1975 – 1995. But somehow, in the long run we have ended up in a better place. My point is that scientific consensus arises from an odd and sometimes unpredictable mixture of theory and evidence and it is not always clear what is right and what is wrong until you can look back from a distance. And despite all the fuzziness and error in the process, progress marches on.

Reproducibility crisis: How do we know how much science replicates?

Literature on the “reproducibility crisis” is increasing although not rapidly enough to bring much empirical clarity to the situation. It remains uncertain how much published science is irreproducible and whether the proportion, whatever it may be, constitutes a crisis. And like small children, unable to wait for the second marshmallow, some scientists in my twitter feed seem to have grown tired of attempting to answer these questions via the usual scientific methods; rather they are declaring in louder and louder voices that there IS a reproducibility crisis as if they can settle these questions by brute force. They have been reduced in the past few days to, I kid you not, (1) twitter polls; (2) arguing about whether 0 is a number; and most egregiously, (3) declaring that “sowing doubt” is akin to being a climate change denier.

Given that the questions at hand here have not at all been tested in the manner of climate science to yield such a consensus, this latter tactic is so outrageously beyond the pale, I am giving over my blog to comment on the reproducibility crisis for some time, writing willy-nilly as the mood hits me on topics such as its apparent size, its nature, its causes, its consequences and the proposed solutions. Keeping in mind that the readers of my blog are usually researchers in communication sciences and disorders, as well as some speech language pathologists, I will bring the topic home to speech research each time. I promise that although there may be numbers there will be no math, I leave the technical aspects to others as it is the philosophical and practical aspects of the question that concern me.

Even though I am in no mind to be logical about this at all, let’s start at the beginning, (unless you think this is the end, which would not be unreasonable). Is there in fact a consensus that that there is a reproducibility crisis? I will leave aside for the moment the fact that there is not even a consensus about what the word “reproducibility” means or what exactly to call this crisis. Notwithstanding this basic problem with concepts and categories, the evidence for the notion that there is a crisis comes from three lines of data: (1) estimates of what proportion of science can be replicated, that is if you reproduce the methods of a study with different but similar participants, are the original results confirmed or replicated; (2) survey results of scientists’ opinions about how much science can be reproduced and whether reproducibility is a crisis or not; and less frequently (3) efforts to determine whether the current rate of reproducibility or irreproducibility is a problem for scientific progress itself.

I am going to start with the first point and carry on to the others in later posts so as not to go on too long (because I am aware there is nothing new to be said really, it is just that it is hard to hear over the shouting about the consensus we are all having). I have no opinion on how much science can be replicated. I laughed when I saw the question posed in a recent Nature poll “In your opinion, what proportion of published results in your field are reproducible?” (notice that the response alternatives were percentages from 0 to 100% in increments of 10 with no “don’t know” option). The idea that people answered this! For myself I would simply have no basis for answering the question.  I say this as a person who is as well read in my field as anyone, after 30 years of research and 2 substantive books. So faced with it, I would have no choice but to abandon the poll because being a scientist, my first rule is don’t  make shit up. It’s a ridiculous question to ask anyone who has not set out to answer it specifically. But if I were to set out to answer it, I would have to approach it like any other scientific problem by asking first, what are the major concepts in the question? How can they be operationalized? How are they typically operationalized? Is there a consensus on those definitions and methods? And then having solved the basic measurement problems I would ask what are the best methods to tackle the problem. We are far from settling any of these issues in this domain and therefore it is patently false to claim that we have a consensus on the answer!

The big questions that strike me as problematic are what counts as a “published result,” more importantly what counts as a “representative sample” of published results, and finally, what counts as a “replication”. Without rehashing all the back-and-forth in Bishop’s blog and the argument that many are so familiar with we know that there is a lot of disagreement about the different ways in which these questions might be answered and what the answer might be. Currently we have estimates on the table for “how much science can be replicated” that range from “quite high” (based on back of the envelope calculations), through 30 to 47%ish (based on actual empirical efforts to replicate weird collections of findings) through finally, Ioannidis’ (2005) wonderfully trendy conclusion that “most published research findings are false” based on simulations. I do not know the answer to this question. And even if I did, I wouldn’t know how to evaluate it because I have no idea how much replication is the right amount when it comes to ensuring scientific progress. I will come back to that on another day. But for now my point is this: there is no consensus on how much published science can be replicated. And there is no consensus on how low that number needs to go before we have an actual crisis. Claiming that there is so much consensus that raising questions about the answers to these questions is akin to heresy is ridiculous and sad. Because there is one thing I do know: Scientists get to ask questions. That is what we do. More importantly, we answer them. And we especially don’t pretend to have found the answers when we have barely started to look.

I promised to put a little speech therapy into this blog so here it is. The Open Science Collaboration said reasonably that there “is no single standard for evaluating replication success. Here, we evaluated reproducibility using significance and P values, effect sizes, subjective assessments of replication teams, and meta-analysis of effect sizes.” More substantively, even if a research team picks an indicator there is disagreement about how to use it. Take effect size for example: it is not clear to me why replication attempts are expect to replicate the size of the effect size that is observed in the original study or even how one does that exactly. There is a lot of argument about that nonetheless which makes it hard to decide whether a finding has been replicated or not. How to determine whether a finding has been confirmed or replicated is not a trivial issue. I grapple with replication of my own work all the time because I develop interventions and I really want to be sure that they work. But even a small randomized controlled trial costs me seven to ten years of effort from getting funds through publication, explaining why I have accomplished only five of these in my career. Therefore, confirming my own work is no easy matter. I always hope someone else will replicate one of those trials but usually if someone has that many resources, they work on their own pet intervention, not mine. So lately I have been working on a design that makes it easier (not easy!) to test and replicate interventions on small groups of participants. It is called the single subject randomization design.

Here is some data that I will be submitting for publication soon. We treated six children with Childhood Apraxia of Speech, using an approach that involved auditory-motor integration prepractice plus normal intense speech practice (AMI). We expected it to be better than just intense speech practice alone, our neutral usual-care control condition (CTL). We also expected it to be better than an alternative treatment that is contra-indicated for kids with this diagnosis (PMP). We repeated the experiment exactly using a single subject randomization design over 6 children and then pooled the p values. All the appropriate controls for internal validity were employed (randomization with concealment, blinding and so on). The point from the perspective of this blog is that there are different kinds of information to evaluate the results, the effect sizes, the confidence intervals for the effect sizes, the p values, and the pooled p values. So, from the point of view of the reproducibility project, these are my questions: (1) how many findings will I publish here? (2) how many times did I replicate my own finding(s)?

TASC MP Group