2.1 Incentives and coopetition: Leaderboards considered harmful

It is a cliche that whatever you measure, you get. Leaderboards emphasize winners and losers. If you do a Google search for “meme: mine is bigger than yours,” you will find a bunch of rude, childish, and even dangerous images of nuclear brinkmanship. International relations and science should be better than school boys playing king-of-the-hill. Hopefully, there is more to the literature than boys being boys.

TREC^{Footnote c} (Text REtrieval Conference) emphasizes coopetition.^{Footnote d} (Voorhees Reference Voorhees2021) as opposed competition. In her keynote at SIGIR-2020,^{Footnote e} as well as her invited talk at the ACL-2021 Workshop on Benchmarking,^{Footnote f} Voorhees observed that:

• • competing may give you a bigger piece of the pie …

• • … while cooperation makes the whole pie bigger ^{Footnote g}

TREC participants are asked to sign a form that forbids explicit advertising of TREC results. This prohibition was mentioned a number of times in the videos of the 25th anniversary of TREC.^{Footnote h} While participants appreciate the principle, the temptation to boast is difficult to resist.

Voorhees is making an important point. Consider the overview paper to the TREC Deep Learning track.^{Footnote i} (Craswell et al. Reference Craswell, Mitra, Yilmaz, Campos and Voorhees2020), for example, where methods are split into three types: nnlm (neural net language models such as BERT), nn (other types of neural nets), and trad (traditional methods). Their Figure 1 shows performance is best for nnlm and worst for trad. That is, nnlm $>$ nn $>$ trad. In this way, coopetition produces important insights that advance the field in meaningful ways, in contrast with leaderboards that emphasize competition and schoolyard nonsense such as “mine is bigger than yours.”

Figure 1. Default search concepts for ACL-2021, according to semantic paths (see footnote Footnote al).

As a second example of coopetition and competition, consider MRQA (Machine Reading for Question Answering) (Fisch et al. Reference Fisch, Talmor, Jia, Seo, Choi and Chen2019). The call for papers^{Footnote j} highlights a number of admirable objectives such as domain transfer, interpretability, robustness, and error analysis, but unfortunately, the shared task^{Footnote k} leads with a leaderboard and congratulates the winners, with no mention of the more admirable objectives.

With a slightly different design, the shared task could have provided some interesting insights into domain transfer. Table 1 of (Fisch et al. Reference Fisch, Talmor, Jia, Seo, Choi and Chen2019) lists 18 QA benchmarks, split up into three groups of six benchmarks. The three groups are used for train, validation, and test, respectively. Suppose instead of using this train/validation/test split, we used a number of different splits. Could we learn that transfer is more successful for some splits than others?

Table 1. ACL-2021 topics, sorted by the number of senior area chairs (SACs) and area chairs (ACs), based on footnote Footnote ai

MRQA identifies some interesting similarities and differences among the 18 benchmarks:

• • source of documents: Wikipedia/Web snippets/misc

  • – Wikipedia (7 benchmarks): DROP, HotpotQA, QAMR, RelationExtraction, SQuAD, TREC, Natural Questions

  • – Web snippets (3 benchmarks): TriviaQA, SearchQA, ComplexWebQ

  • – misc (8 benchmarks): MCTest, RACE, DuoRC, NewsQA, BioASQ, QAST, BioProcess, TextbookQA

• • source of questions: Crowdsourced/Domain Experts/misc

  • – Crowdsourced (9 benchmarks): ComplexWebQ, DROP, DuoRC, HotpotQA, MCTest, NewsQA, QAMR, SQuAD, TREC

  • – Domain Experts (5 benchmarks): BioASQ, BioProcess, QAST, RACE, TextbookQA

  • – misc (4 benchmarks): SearchQA, Questions Natural, RelationExtraction, TriviaQA

• • source of answers: based on documents/not based on documents

  • – based on documents (9 benchmarks): SQuAD HotpotQA, DROP, RACE, TextbookQA, BioProcess, MCTest, QAMR, QAST

  • – not based on documents (9 benchmarks): NewsQA TriviaQA, SearchQA, Natural Questions, BioASQ, DuoRC, RelationExtraction, ComplexWebQ, TREC

It would be very interesting to know if these patterns are important for transfer or not. There is pretty clear evidence, for example, that constructed (crowdsourced) questions are easier than questions from query logs. TREC QA,^{Footnote l} for example, started with “constructed” questions in 1999, but quickly moved to “real” questions from query logs for subsequent TREC QA tracks (2000–2007) because constructed questions are too easy for systems and unrealistic (Voorhees Reference Voorhees2001). Based on these observations, transfer might also be more effective between benchmarks that are similar to one another in terms of the source of questions, documents, and/or answers. In this way, coopetition could produce important insights that advance the field in more meaningful ways than leaderboards and competition.

It also helps to advance the field when benchmarks are realistic. Most of the benchmarks in MRQA are based on benchmarks from academia, except for Natural Questions. To construct more realistic benchmarks, it is advisable to work with industry and make sure the benchmark is representative of a real problem that they care about. A number of companies have been involved in a number of benchmark efforts:

• • Microsoft Bing: TREC Web track^{Footnote m} (1999–2014), TREC Deep Learning track^{Footnote n} (Craswell et al. Reference Craswell, Mitra, Yilmaz, Campos and Voorhees2020)

• • Baidu: DuReader^{Footnote o} (He et al. Reference He, Liu, Liu, Lyu, Zhao, Xiao, Liu, Wang, Wu, She, Liu, Wu and Wang2018)

• • Google: Natural Questions^{Footnote p} (Kwiatkowski et al. Reference Kwiatkowski, Palomaki, Redfield, Collins, Parikh, Alberti, Epstein, Polosukhin, Devlin, Lee, Toutanova, Jones, Kelcey, Chang, Dai, Uszkoreit, Le and Petrov2019)

There are also connections between the TREC QA track^{Footnote q} (1999–2007) and IBM Watson Jeopardy! In this case, IBM started in 2006 with a system designed for the TREC QA track and discovered that that system did not work well enough for Jeopardy questions,^{Footnote r} as discussed at a celebration for the 25th anniversary of TREC.^{Footnote s} After 5 years of hard work, the IBM system beat the two best human Jeopardy players in 2011, but their 2011 system was probably very different from their 2006 system because, among other things, the TREC QA tasks are not very representative of the Jeopardy task. The Jeopardy task is a problem that matters to IBM marketing, though problems such as web search are probably more real than Jeopardy.^{Footnote t}

Unfortunately, while we all know that IBM won, much less is remembered about how that was accomplished (Ferrucci et al. Reference Ferrucci, Brown, Chu-Carroll, Fan, Gondek, Kalyanpur, Lally, Murdock, Nyberg, Prager, Schlaefer and Welty2010; Ferrucci Reference Ferrucci2012), and how that achievement could have advanced the field toward more admirable goals. We should follow Voorhees’s advice and replace competition with coopetition. The point is not who wins, but insights that advance the field.

2.2 Sucking the oxygen out of the room

What is not happening as a result of too much SOTA-chasing? It is becoming harder and harder to publish computational linguistics in a conference on computational linguistics. Students preparing for their first ACL paper may find textbooks on machine learning: (Bishop Reference Bishop2016; Goodfellow et al. Reference Goodfellow, Bengio and Courville2016) to be more helpful than textbooks on computational linguistics: (Manning and Schutze Reference Manning and Schutze1999; Jurafsky Reference Jurafsky2000; Eisenstein Reference Eisenstein2019) and handbooks (Dale et al. Reference Dale, Moisl and Somers2000; Mitkov Reference Mitkov2003; Clark et al. Reference Clark, Fox and Lappin2013).

ACL conferences used to be more inclusive. We used to see more people at our meetings from more fields such as linguistics, philosophy, lexicography, psychology, etc. ACL venues used to reach out to HLT (human language technology), a combination of computational linguistics, speech and information retrieval/web search. Lots of people used to publish in more combinations of fields/venues: computational linguistics (ACL, EMNLP, NAACL, EACL, Coling), Machine Learning (NeurIPS), Speech (ICASSP,^{Footnote u} Interspeech^{Footnote v}), Information Retrieval (SIGIR,^{Footnote w} TREC), Web Search (WWW,^{Footnote x} WSDM^{Footnote y}), Datamining (KDD^{Footnote z}), Language Resources (LREC^{Footnote aa}), etc.

Why do we no longer see these people at ACL? It became clear to us that many of them no longer feel welcome when we attended an ACL-2014 workshop in honor of Chuck Fillmore.^{Footnote ab} The workshop was bitter sweet. They were grateful that Chuck won a Lifetime Achievement Award,^{Footnote ac} but they were also mourning his passing, and there were concerns about the relevancy of their work to where ACL was going. Fillmore’s “Case for Case” (Fillmore Reference Fillmore, Bach and Harms1968) has more than 11k citations in Google Scholar, but ACL is no longer interested in this approach, or in linguistic resources such as FrameNet (and much of what is discussed at LREC).

Reviewers, these days, sometimes suggest that resources such as FrameNet and WordNet are no longer relevant now that BERT works as well as it does. Such remarks discourage diversity. People who have invested in resources may find such remarks offensive (and unethical).

Even people in Machine Learning have reservations about SOTA-chasing. Rahimi gave a Test of Time Award talk at NIPS-2017 titled “Machine Learning has become Alchemy.”^{Footnote ad} NIPS (now called NeurIPS) used to be more receptive to theory and what Rahimi referred to as the rigor police. Apparently, SOTA-chasing is squeezing out many important topics including theory and computational linguistics.

There is a different kind of rigor in other fields such as Lexicography, Library Science, and Information Retrieval, where proper attribution is taken very seriously. People in these fields care deeply about sampling (balance), what came from where, and what is representative of what. They will feel unwelcome when SOTA-chasing moves too quickly with less rigor. Consider the reference to TREC in HuggingFace^{Footnote ae} as well as Table 1 of MRQA (Fisch et al. Reference Fisch, Talmor, Jia, Seo, Choi and Chen2019), as discussed in Section 2.1. There have been 30 text retrieval conferences (TREC)^{Footnote af} thus far. For each of those 30 conferences, there are many tracks and many datasets with many contributions from many people. We asked someone familiar with TREC for help disambiguating the references to TREC in HuggingFace and MRQA. The response was uncharacteristically sharp:

It is important, especially in certain fields, to give credit where credit is due. Citing work with proper attributions will make our field more inclusive and more attractive to people in other fields with different priorities and diverse views of rigor. Proper citations will also facilitate replication.

2.3 Unrealistic expectations: Superhuman performance, seriously???

We now turn to the third of the three costs of SOTA-chasing mentioned at the beginning of Section 2. Claims of superhuman performance (on tasks that appear to be more realistic than they are) create unrealistic expectations that could lead to an AI winter.

It is not hard to construct CAPTCHAs (Completely Automated Public Turing test to tell Computers and Humans Apart)^{Footnote ar} as well as the reverse, which we call reverse CAPTCHAs. For standard CAPTCHAs, you can bet on people to succeed and machines to fail, whereas for reverse CAPTCHAs, you can bet on machines to succeed and people to fail.

Technology is often amazing, though sometimes exhausting, embarrassing, unethical, and/or dangerous. It is easy to find examples in the news and in social media of amusing/scary “computer errors.” Alexa recently told a 10-year-old girl to do something dangerous with a penny and electricity.^{Footnote as},^{Footnote at} Gmail autocorrect recently sent an embarrassing email where an interest in speaking with a business associate somehow came out as an interest in sleeping with the business associate.

Computers are being used for all sorts of use cases, raising some serious ethical questions (O’Neil Reference O’Neil2016). In one case, a judge ruled that Google translate is not good enough to count as consent for a police search.^{Footnote au} Society will need to address many more ethical questions like this.

If machines were actually better than people at transcribing speech and machine translation, then why are there so many “computer errors” in captions for services such as YouTube and Zoom? There is always more work to do. There are a few tasks, like playing chess, where computers are much better than people. But there are many tasks that are important for commercial applications, like captions, where there are opportunities for improvement.

There have been claims at WMT (Workshop on Machine Translation) (Barrault et al. Reference Barrault, Bojar, Costa-jussÀ, Federmann, Fishel, Graham, Haddow, Huck, Koehn, Malmasi, Monz, MÜller, Pal, Post and Zampieri2019) and elsewhere suggesting machines have achieved more than they have (parity/superhuman performance). The community tends to remember this simple take-away message, despite reassessments (Toral Reference Toral2020), and cautionary caveats such as this:

Replication is a major problem for many fields, as will be discussed in Section 4 on the replication crisis. One of the root causes behind the replication crisis is over-confidence in the scientific method.

Evaluations can also be misleading because of over-confidence in the methodology and metrics such as BLEU. The community is more likely to remember the superhuman result than cautionary caveats/reassessments such as your mileage may vary (YMMV).^{Footnote av}

Consider technology for translating meetings, for example. This technology is amazingly good, but far from human parity. The first author has considerable experience with this technology because he works for a Chinese company and does not speak Chinese. When he has access to a human interpreter, he is much more engaged in the meeting (and not nearly as exhausted).

When this technology was first introduced, everyone was impressed with how well it worked. The live stream was displayed on stage so everyone in the room could read whatever was said over the house speakers in real time in both English and Chinese. The chair of one high-profile session made a point to call out the technology.^{Footnote aw}

Now that the technology has been around for a few years, the technology is no longer displayed on stage (perhaps because of a few inevitable embarrassing mistakes). The latest version runs on phones, so only those of us who need the technology can see (and hear) everything (warts and all) in both English and Chinese. The technology is even better than it used to be, especially with respect to latency, but even so, it is far from human parity.

Others who do not use the technology as much as we do may be misled by evaluations that report superhuman BLEU scores and latency. While the machine may be better than people in those terms, BLEU and latency are not the terms that matter. Professional interpreters translate what needs to be said when it needs to be said, and human interpreters do not make “computer errors.”

We can correct some computer errors. For example, when the machine says “ecology” in a Baidu meeting, the speaker is probably talking about “eco-systems.” Other computer errors are more challenging. One time, we guessed the machine made an error when it used a politically sensitive word. We asked for clarification after the meeting. In this case, it turned out that the translation was actually correct, but the context was “lost in translation.” When we have access to a human interpreter, there are more opportunities to ask for clarifications and less need to do so.

Given realities such as these, when evaluations produce numbers that are too good to be true (using inappropriate metrics such as BLEU and average latency), why do we take these numbers so seriously? We have so much confidence in our evaluation methodology that we believe the results (and gloss over caveats/reassessments), even when we know the results cannot be right:

A number of evaluations are reporting that machines are better than people on a number of tasks^{Footnote ay},^{Footnote az},^{Footnote ba},^{Footnote bb},^{Footnote bc},^{Footnote bd} (Nangia and Bowman Reference Nangia and Bowman2019; Nguyen et al. Reference Nguyen, Stueker and Waibel2021). We all know these superhuman numbers are too good to be true and unlikely to transfer beyond academic benchmarks to tasks that matter for commercial practice. No one will remember the caveats/reassessments, but they will remember the unrealistic expectations, and that will not be good for the long-term health of the field.

Viewed in this way, the successes of deep nets on so many benchmarks could be interpreted as a criticism of these benchmarks. Benchmarks tend to focus too much on tasks that are ideal for technologies we already have. But benchmarks should place greater emphasis on opportunities for improvement. Benchmarks should be different from PR hype. The point of benchmarks is not to make our technology look good (or better than it is), but to help set the agenda for future work. Evaluations provide credible measurements of progress, as well as realistic expectations for the future.

We are not objecting to evaluation, and measuring real progress. But we are objecting to “gains” that are more noise/hope/hype than progress. The difference between the top two places on a leaderboard may not be significant or replicable or interesting.

3.1 SOTA-chasing: A consequence of a lack of leadership

SOTA-chasing may have evolved out of the evaluation tradition, which has a long history. (Raji et al. Reference Raji, Bender, Paullada, Denton and Hanna2021) start by summarizing some of this history in (Lewis and Crews Reference Lewis and Crews1985; Liberman Reference Liberman2010; Church Reference Church2018a). Historically, there was a point to the emphasis on evaluation; evaluation used to be more than pointless SOTA-chasing.

Many first-hand accounts of this history were presented at the ACL-2021 Workshop on Benchmarking: Past, Present, and Future (BPPF) (Church et al. Reference Church, Liberman and Kordoni2021a). Videos and slides are posted on github.^{Footnote bg}

Much of this history involves influential leaders such as John Mashey, Fred Jelinek, and Charles Wayne, as will be discussed in Section 3.1.1. Before Mashey, Jelinek and Wayne, the agenda was largely set by many other influential leaders: Pierce, Skinner, Shannon, Licklider, Minsky, Chomsky, and others (Church Reference Church2011). These days, one might try to argue that the agenda is coming top-down from Turing Award Winners such as Hinton, Bengio, LeCun, Pearl, and others. Bengio, for example, is working on some long-standing hard problems in Artificial Intelligence such as causality^{Footnote bh} (Bengio et al. Reference Bengio, Deleu, Rahaman, Ke, Lachapelle, Bilaniuk, Goyal and Pal2019; SchÖlkopf et al. Reference SchÖlkopf, Locatello, Bauer, Ke, Kalchbrenner, Goyal and Bengio2021) and compositionality.^{Footnote bi} Despite such top-down efforts, though, we view SOTA-chasing as evidence that the agenda is, in fact, emerging more bottom-up from community-driven sources such as papers with code (PWC) and HuggingFace.

This paper will suggest that SOTA-chasing is a consequence of a lack of top-down leadership. Students need help finding projects to work on. Success is measured transactionally. What does it take to get a paper accepted in the next conference? Publish or perish. Unless we offer a more promising alternative, students are likely to turn to PWC to find a project that is likely to “succeed” in the next round of conference reviews. Long-term success is more of a concern for more established researchers with more experience and more responsibility for the long-term health of the field.

Established researchers, such as authors of textbooks, used to play more of a role in setting the agenda. The connection between textbooks (Manning and Schutze Reference Manning and Schutze1999; Jurafsky Reference Jurafsky2000; Eisenstein Reference Eisenstein2019) and ACL meetings used to be stronger than it is today, as discussed in Section 2.2.

These days, the agenda is determined more bottom-up by mouse clicks. Everyone has an equal vote. The author of a textbook has no more vote than a student just starting out. Consequently, short-term concerns tend to dominate long-term concerns since the voting block of students starting out is much larger than the relatively small number of established researchers. The agenda is no longer determined by authors of textbooks and influencers such as John Mashey, Fred Jelinek and Charles Wayne.

3.2 SOTA-chasing: A consequence of poor reviewing processes

In addition to a lack of leadership, another root cause of SOTA-chasing is poor reviewing processes. Rogers’s blog attributes SOTA-chasing to lazy/poor reviewing, information overload (drowning in papers), and glorification of benchmarks, though there is more discussion of poor reviewing in her blog than glorification of benchmarks. Her blog leads with the following tweet:^{Footnote bu}

It is a shame that EMNLP reviewing is as bad as it is. EMNLP’s poor reviewing is particularly ironic given that we created EMNLP largely as a reaction to ACL’s poor reviewing, as discussed in Section 1.2 of (Church Reference Church2020). EMNLP reviewing is used to be quicker than ACL by construction.^{Footnote bv} These days, EMNLP reviewing is no quicker (and no better) since all ACL* conferences use the same (broken) processes. Putting all our eggs in one basket is not a solution, especially if the basket is known to be defective.

There have been many criticisms of reviewing recently. Rogers’s blog offers a number of constructive suggestions to reviewers. While we agree that reviewing is bad, and even worse than it used to be, blaming the reviewers is unlikely to lead to improvements. Reviewers do what reviewers do. Creating more tutorials,^{Footnote bw} rules and process are unlikely to help.

It is widely agreed that ACL reviewing is an opportunity for improvement. The ACL has recently rolled out a new rolling review process (ARR)^{Footnote bx} based on open review. Perhaps ARR will improve matters, though we have serious doubts.

Best practices tend to start by identifying root cause(s). Introducing change for change sake is unlikely to lead to improvements. Roll out new processes gradually; do not make too many changes at the same time.

One thing is certain: as shown in Table 2, ACL-2022 is no faster than ACL-2021. It is claimed that ARR is faster:

Table 2. ACL-2022 (after ARR) is no faster than ACL-2021 (before ARR)

but ACL-2022 used ARR and ACL-2021 did not. If ARR really was 3x faster, why doesn’t that speed up show up in the schedules in Table 2?

Speed is important, but quality is even more important. Why is reviewing so bad? Reviewers are tired and underpaid, as Rogers points out in her blog. But that is also true of researchers. Most of us do what we do because we care deeply about what we do. Researchers are also tired and underpaid. That is not the root cause for bad reviewing.

A more likely root cause is the assignment of papers to reviewers. ARR has a number of serious design flaws that make it very likely that reviewers will be less qualified/sympathetic than they used to be. It used to be rare for students to be invited to review. Reviewers were typically authors of cited papers, increasing the odds that reviewers would be familiar with relevant background material, and positively inclined toward the general approach. Reviewers used to have more expertise in the topic than the target audience for the paper. Unfortunately, that is no longer the case.

It appears that ARR automates the assignment of papers too much. In Section 2.7.1 of (Church Reference Church2020), we discussed a number of common methods for assigning papers to reviewers:

1. 1. Delegate to authors (keywords)

2. 2. Delegate to reviewers (bidding)

3. 3. Delegate to middle management (manual assignments)

4. 4. Delegate to software using automated routing (Yarowsky and Florian Reference Yarowsky and Florian1999)

5. 5. Semi-automatic routing (automatic routing with manual post-editing).

ARR uses automatic routing with too little post-editing. Action editors are asked to over-ride initial assignments,^{Footnote bz} but this process is unworkable because of fluctuations in the workload. There were just barely enough AEs for the October-2021 round of ARR, but not nearly enough for November 2021 because of a submission deadline for ACL-2022.

To make matters worse, ARR eliminated areas, a huge mistake in our opinion, because action editors cannot be expected to know who’s who and what’s what in all areas.

We prefer a recursive structure where papers are assigned to subcommittees going down the tree, until the number of papers is small enough that a subcommittee can handle the load. With this structure, the subcommittee chair can be expected to know who’s who and what’s what in their subarea. Chairs should be encouraged to send papers back up the tree if they receive papers that go beyond their expertise.

There are some obvious weaknesses with automatic routing and the ARR process. We described our experience with (Yarowsky and Florian Reference Yarowsky and Florian1999) in (Church Reference Church2020). Automatic routing loves conflicts of interest. If there is a way to send a paper to reviewers with conflicts of interest, automatic routing programs will do just that.

Since ACL-2022 makes it possible to see the names of the other reviewers, we can check for conflicts of interest. ACL-2022 assigned one paper to two reviewers that work closely together. When we complained to the meta-reviewer, after apologizing for taking a long time to reply (because the system was sending too many unimportant emails), the meta-reviewer made it clear that there are too many such conflicts to fix.

Perhaps ARR chose to use automatic routing to cope with the scale. This is not a good reason though. The routing process is extremely important. If a paper is sent to an unqualified/unsympathetic reviewer, then the reviewer is likely to essentially “abstain” and kill the paper with an average/low score.

Automating the routing process is disrespectful to authors and reviewers and the community. Reviewers do not like to review papers outside their area. Authors work hard on their submissions. We owe them more than “abstentions.” The community deserves to know that published papers have been credibly reviewed by qualified reviewers with considerably more expertise in the area than the target audience. It is a violation of ethics to route papers the way we do without a reasonable number of qualified experts involved in the routing process.

Why does ARR believe that it is necessary to automate the process? Scale was mentioned above. ACL does receive quite a few submissions. There were about 3000 submissions in November 2021, about an order of magnitude more than we had for EMNLP in 1999. For EMNLP-1999, the first author assigned each paper to a subcommittee in two days, at a rate of 2 minutes per paper. Those subcommittees would then assign papers to reviewers.

This process is embarrassingly parallel. Thus, with about ten people doing what the first author did for EMNLP-1999, we could route the 3000 papers to subcommittees in two days. The process also scales recursively. If a subcommittee receives too many papers, we can split the subcommittee recursively into subcommittees, as needed. The entire routing process should require no more than a week.

In principle, the law of large numbers should make it easier to find good matches between papers and reviewers. Scale is not an excuse for disrespecting authors and reviewers.

To make matters even worse, ARR uses the wrong population to sample reviewers. Now that all authors are required to review, including students^{Footnote ca} and authors from other areas, it is very likely that reviewers will be unqualified and unmotivated. The process should sample reviewers from the population of published/cited papers, not submitted papers.

Chairs are always looking for more reviewers. Selecting reviewers from cited papers should help since the set of cited papers is much larger than the set of submitted papers.^{Footnote cb}

There had been some talk when ARR was first proposed about minimum requirements for reviewers in terms of h-index and/or publications, but since ARR makes it easy to see the names of other reviewers, it is easy to verify that many/most of reviewers are not as qualified as they were a few decades ago.

SOTA-chasing is a natural consequence of these new (but not improved) processes. Since authors cannot assume that reviewers are qualified or sympathetic to the area, authors need to come up with a simple argument that will work with unmotivated reviewers. Empirically, authors have discovered that SOTA-chasing is effective with random reviewers.

We cannot blame authors for doing what they are doing. Nor can we blame reviewers for doing what they are doing. We have seen the problem, and it is us.